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One-Step Generalization Ratio Guided Optimization for Domain Generalization | Accept (oral) | Summary: The paper presents GENIE (Generalization-ENhancing Iterative Equalizer), an optimizer aimed at improving domain generalization (DG) by using the One-Step Generalization Ratio (OSGR). GENIE dynamically equalizes the contribution of each parameter to loss reduction, preventing overfitting to domain-specific features. The optimizer incorporates preconditioning, noise injection, and random dropout to stabilize updates and promote domain-invariant feature learning. Experimental results show that GENIE outperforms existing optimizers like SGD, Adam, and SAM on DG benchmarks, offering improved generalization without requiring changes to model architecture. GENIE is applicable to various tasks such as DG and single-domain generalization.
Claims And Evidence: Yes, the claims made in the submission are generally supported by clear and convincing evidence.
GENIE's Effectiveness: The paper claims that GENIE outperforms existing optimizers like SGD, Adam, and SAM in domain generalization tasks. This claim is supported by extensive empirical evidence from experiments on several widely-used domain generalization benchmarks (PACS, VLCS, OfficeHome, etc.). The results show that GENIE consistently achieves higher performance than these optimizers, which provides strong evidence for its effectiveness.
OSGR as a Valid Metric: The paper claims that the One-Step Generalization Ratio (OSGR) effectively measures the generalization capacity of the optimizer. The authors support this claim with both theoretical analysis and empirical validation, demonstrating that GENIE's preconditioning leads to a higher OSGR, which correlates with better generalization.
Preconditioning and Parameter Balance: The claim that GENIE's preconditioning strategy promotes balanced parameter updates and mitigates overfitting is backed by a detailed theoretical framework and experimental results. The authors present a clear rationale for how the preconditioning factor adjusts OSGR dynamically, leading to more stable and robust learning.
Computational Efficiency: The paper claims that GENIE is computationally efficient, offering faster training times compared to SAM. The evidence provided, in the form of training time comparisons, supports this claim by showing that GENIE achieves better performance in less time, especially in comparison to optimizers like SAM, which require more computational overhead.
Potential Issues:
Generalization to Other Datasets: While GENIE performs well on several benchmarks, the paper does not address its performance on datasets with more extreme or non-standard domain shifts. Testing GENIE on additional challenging datasets might provide more comprehensive evidence of its generalizability.
Impact of Preconditioning: The effectiveness of the preconditioning term is theoretically explained but could benefit from further clarity or empirical validation on how it compares to other domain generalization techniques. Additional experiments could clarify the impact of preconditioning in different scenarios.
Overall, the claims are well-supported, with clear experimental results and solid theoretical backing. However, some additional tests and more detailed comparisons with other methods could further strengthen the evidence.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense for the problem at hand.
Proposed Method (GENIE): The proposed method, GENIE, is well-suited for addressing the challenges of domain generalization (DG). By incorporating the One-Step Generalization Ratio (OSGR) and using preconditioning, noise injection, and random dropout masks, the method tackles the problem of domain-specific overfitting and promotes robust, domain-invariant feature learning. This approach is aligned with the core issue in DG, which is ensuring that models generalize well to unseen domains without overfitting to spurious correlations.
Evaluation Criteria (OSGR and Benchmark Datasets): The use of OSGR as an evaluation metric is appropriate, as it directly quantifies the contribution of model updates to generalization. The paper demonstrates that higher OSGR correlates with better generalization performance, making it a valuable tool for assessing domain generalization methods. Additionally, the use of widely accepted benchmark datasets like PACS, VLCS, and OfficeHome is a sensible choice, as these datasets are commonly used in DG research and provide a solid basis for comparison with other methods.
Overall, the proposed methods and evaluation criteria are both relevant and effective for tackling the problem of domain generalization and ensuring that the results are comparable with existing approaches in the field.
Theoretical Claims: Theoretical claims in the paper are based on sound reasoning, and the authors provide a thorough mathematical foundation for the proposed GENIE optimizer. However, as a reviewer, I have not verified the correctness of the proofs in detail. The paper includes several theoretical claims, such as the connection between OSGR and parameter-wise statistics (Theorem 3.1), convergence analysis (Theorem 3.9), and the impact of preconditioning on OSGR (Corollary 3.2).
Theorem 3.1 establishes the relationship between gradient updates and generalization, introducing the concept of Gradient Signal-to-Noise Ratio (GSNR). This is a critical part of the theoretical framework, but it would be beneficial to further break down the derivations to ensure all steps in the proof are clear and rigorous.
Theorem 3.9 provides a convergence rate analysis under certain assumptions. While the theorem is mathematically sound, the assumptions (such as bounded gradients and smooth loss functions) are typical for optimization in deep learning. However, some of these assumptions may not always hold in all practical scenarios, and this could potentially limit the generalizability of the theoretical results.
Corollary 3.2 discusses how preconditioning affects OSGR. The logic behind this corollary is solid, but again, further clarification and empirical validation of how preconditioning impacts OSGR in various scenarios would strengthen the argument.
Overall, the theoretical claims are well-founded and supported by proofs, but a deeper verification and potential clarification of the proof steps would be helpful for ensuring their correctness.
Experimental Designs Or Analyses: Yes, the experimental designs and analyses presented in the paper generally appear sound and valid. The authors conduct several key experiments to evaluate the effectiveness of the GENIE optimizer, and the results are based on widely accepted benchmark datasets, which ensures that the findings are relevant and comparable to existing work in the domain.
Evaluation on Benchmark Datasets: The authors evaluate GENIE on well-established datasets such as PACS, VLCS, and OfficeHome. These datasets are commonly used in domain generalization (DG) research, which makes the experimental setup reliable. The results consistently show that GENIE outperforms other optimizers like SGD, Adam, and SAM. This approach provides a robust comparison of GENIE's performance across multiple standard datasets, ensuring the validity of the results.
Comparison with Other Optimizers: The paper compares GENIE with various baseline optimizers, including SGD, Adam, AdamW, and SAM. This is a solid experimental design, as it allows the authors to clearly show how GENIE improves performance over existing methods. The statistical significance of these comparisons could be strengthened if the authors provided more detailed metrics, such as p-values, to further support the claim that GENIE outperforms these optimizers.
Training Time and Computational Efficiency: The authors also conduct experiments to compare training times across different optimizers. GENIE consistently performs better than SAM in terms of training time, which supports the claim that it is computationally more efficient. However, additional experiments on more complex models or larger datasets could provide further insight into the scalability and efficiency of GENIE in real-world applications.
Ablation Study: The paper includes an ablation study to examine the impact of GENIE's individual components, such as preconditioning, noise injection, and random dropout masks. This is a useful and rigorous analysis that helps to isolate the effects of each component. The ablation study design is valid, and it clearly shows that combining all components leads to the best performance.
Potential Issues:
Limited Number of Datasets: While the paper evaluates GENIE on several standard datasets, testing on a broader range of real-world datasets with more diverse domain shifts could further validate the generalizability of the method.
Lack of Statistical Analysis: The experimental results show that GENIE outperforms other optimizers, but including more statistical analysis (e.g., significance testing) would strengthen the argument for its superiority.
Overall, the experimental designs and analyses are robust and well-structured, but additional experiments and statistical analysis could provide further confidence in the generalizability of the findings.
Supplementary Material: Yes, I reviewed the supplementary material, including sections A, B, C, and D. Section A (Notation) provides clarifications on the symbols and mathematical terms used in the paper, which are essential for understanding the theoretical claims and algorithms. Section B (Proof of Theorems) includes the detailed proofs for key theorems such as Theorem 3.1 and Theorem 3.9, offering the theoretical foundation for the GENIE optimizer. Section C (Implementation Details) describes the training setup, hyperparameter tuning, and provides pseudo code for GENIE, explaining its integration with other optimizers. Finally, Section D (Experimental Details and Results) presents detailed results from experiments on domain generalization datasets, demonstrating that GENIE outperforms other optimizers like SGD, Adam, and SAM across various datasets, particularly on challenging datasets such as TerraIncognita. Overall, the supplementary material supports the main claims and enhances the clarity and reproducibility of the study.
Relation To Broader Scientific Literature: The key contributions of this paper build on and extend previous work in the field of domain generalization (DG) and optimization methods. Specifically, the introduction of the GENIE optimizer addresses long-standing challenges in DG, particularly the issue of domain-specific overfitting and generalization across unseen domains.
Connection to Domain Generalization (DG): Previous studies in DG (e.g., Carlucci et al. (2019), Motiian et al. (2017)) have primarily focused on designing models that can generalize well across different domains. However, many of these methods have struggled with issues such as spurious correlations or domain-specific biases. This paper's novel use of the One-Step Generalization Ratio (OSGR) as a metric and optimization strategy represents a step forward by offering a more targeted approach to balance parameter updates, which helps mitigate overfitting to domain-specific features. This builds upon the concept of meta-learning and adversarial training for generalization but introduces an optimization-focused solution.
Relation to Optimization Methods: GENIE also relates to advancements in optimization techniques. Prior works on optimizers like Adam and SAM (e.g., Kingma and Ba (2014), Zhang et al. (2020)) have shown success in improving convergence rates and robustness. However, these methods still face limitations when applied to DG tasks, particularly in dealing with domain shifts. The preconditioning strategy used in GENIE aligns with concepts from adaptive optimizers (like AdaGrad and RMSProp) but offers a more sophisticated approach to achieving balanced gradient updates, making it an important advancement in the optimization landscape.
Ablation and Empirical Results: The paper also contributes to the ongoing research on ablation studies by isolating the effects of specific components such as noise injection, preconditioning, and dropout. Previous works on DG often combine techniques without isolating their individual impacts, making this paper’s clear ablation study a valuable contribution to understanding how each factor influences model performance.
In conclusion, the paper makes significant strides in improving domain generalization through its novel optimizer, GENIE, while also contributing to the broader scientific literature on optimization strategies and domain generalization techniques. It provides a clearer understanding of how optimization approaches can be tailored to address specific challenges in DG and offers insights that can benefit future work in both optimization theory and practical applications in machine learning.
Essential References Not Discussed: While the paper does an excellent job of citing relevant literature, there are a few related works that could strengthen the context for the key contributions, particularly in the areas of domain generalization (DG) and optimization methods. These works are essential for providing a more comprehensive background and for highlighting how the proposed GENIE optimizer fits within the broader research landscape.
Domain Generalization (DG) Approaches:
The paper primarily cites Carlucci et al. (2019) and Motiian et al. (2017), which are foundational in DG, but it misses recent advancements that directly relate to optimizing domain generalization through optimization techniques. For example, Li et al. (2020) introduced Meta-Regularization, which adapts optimization methods for generalization across domains, and this work could provide additional context for the proposed approach. Citing such works would emphasize how GENIE contributes to a broader trend of improving DG through more robust optimization methods.
Optimization for Generalization:
The work on Stochastic Gradient Descent (SGD) and Adam is well covered, but the paper could mention the more recent work on SAM (Sharpness-Aware Minimization) (e.g., Foret et al., 2021), which directly relates to balancing generalization and optimization. SAM has been shown to improve the robustness of models by minimizing sharp minima, which is related to the objectives GENIE aims to achieve with preconditioning. Additionally, there is growing interest in Adaptive Optimization techniques, such as AdaBelief (Zhang et al., 2020), which adaptively correct the update rule based on gradient estimates, and could complement the discussion on GENIE’s preconditioning strategy.
Ablation Studies in Optimization:
The ablation study in the paper is an important contribution, but there is no direct mention of ablation studies in optimization, which have been extensively used in understanding the impact of various components in optimizers. For example, the work by Liu et al. (2021) on the effectiveness of gradient clipping and noise injection in improving model generalization could be cited as it deals with similar experimental setups that focus on mitigating overfitting through different optimization techniques.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your thoughtful and constructive review. We greatly appreciate your insightful comments and the opportunity to clarify several important points you raised.
# Proof Clarity
You suggested additional clarity in the proof derivations, particularly regarding Theorem 3.1. Theorem 3.1 originates from Liu et al. (ICLR 2020), as mentioned in our paper. To maintain brevity, we omitted detailed derivations in the main text. However, in Appendix B.2, we provided a rigorous derivation of Corollary 3.2, which generalizes and clarifies Theorem 3.1. We will ensure this is clearly highlighted in the revised manuscript.
# Impact of Preconditioning on OSGR
Regarding your point on clarifying the impact of preconditioning, Section 3.3.1 (Generalization Analysis) theoretically demonstrates that preconditioning increases OSGR values based on Jensen's inequality. Empirically, Figure 2 shows that GENIE’s preconditioning consistently achieves higher OSGR compared to other optimizers.
Additionally, Table 6's ablation study demonstrates how preconditioning, when combined with dropout and noise injection, enhances generalization performance. Figure 1 further illustrates that GENIE yields a more uniformly distributed gradient update across parameters, clearly supporting our claim that preconditioning effectively balances parameter contributions and improves generalization.
# Comparison with Other Domain Generalization Techniques
In our generalization analysis, we show that the proposed preconditioning—designed to uniformize the OSGR value—leads to improved generalization performance, thereby mathematically supporting our conjecture. To further address the reviewer’s concern regarding comparisons with other methods, we provide a theoretical comparison with Sharpness-Aware Minimization (SAM).
We leverage PAC-Bayesian theory as follows:
$$
E_{\mathcal{S}}\, E_{\theta \sim \widetilde{p}} \left[ R(\theta) \right]
\le
E_{\mathcal{S}}\, E_{\theta \sim \widetilde{p}} \left[
L(\theta) + \frac{\lambda C^2}{8n} + \frac{\mathrm{KL}(\widetilde{p} \| \pi)}{\lambda}
\right]
$$
PAC-Bayesian theory bounds the expected generalization risk by the sum of the empirical risk, a complexity term, and the KL divergence between the posterior $\tilde{p}$ and prior $\pi$. The SAM optimizer focuses on reducing the empirical risk under perturbed parameters (i.e., minimizing local sharpness), while ignoring the KL divergence term. In contrast, our method explicitly improves the generalization bound by minimizing the KL divergence term in a one-step formulation.
In our setting, we define the posterior (the updated parameter distribution) as $\tilde{p} = \mathcal{N}(\theta_t, \Sigma)$ and the prior (previous parameter distribution) as $\pi = \mathcal{N}(\theta_{t+1}, \Sigma)$. Here, the prior can be treated as a data-driven prior which is approximated using all data excluding the current mini-batch. Parameter distributions depend on the distribution of the gradient update with the effective learning rate $\frac{1}{\mathrm{E}[g_j^2]}$.
Taking the derivative of the KL divergence with respect to the gradient-based update, we obtain:
$$
KL(\tilde{p} \| \pi) = \frac{1}{2} \left[ \sum_{i=1}^{J} \frac{\sigma_i^2}{\sigma_i^2} + \sum_{i=1}^{k} \frac{(\theta_{t+1,i} - \theta_{t,i})^2}{\sigma_i^2} - J + \sum_{i=1}^{J} \log\left( \frac{\sigma_i^2}{\sigma_i^2} \right) \right] = \frac{1}{2} \sum_{j=1}^{J} \frac{(\theta_{t+1,j} - \theta_{t,j})^2}{\sigma_j^2}
$$
$$
\left[ \nabla_j \mathrm{KL}(\tilde{p} \| \pi) \right]
= \frac{(\theta_{t+1,j} - \theta_{t,j})}{\sigma_j^2}
= \frac{1}{\mathbb{E}[g_j^2]} \cdot \frac{g_{j,t}}{\sigma_j^2}
= \left( \underset{\mathrm{GENIE}}{ \frac{1}{\mathbb{E}[g_j^2]} \cdot \frac{g_{j,t}^2}{\sigma_j^2} } \right) \cdot \mathrm{sign}(g_{j,t})
$$
This formulation shows that our preconditioning term directly reduces the KL divergence term, thereby contributing to a tighter PAC-Bayesian generalization bound—a benefit not provided by the SAM optimizer.
We sincerely thank you for your detailed and insightful comments, which have significantly helped us strengthen our paper. We hope these clarifications fully address your concerns and further highlight the robustness and contributions of GENIE. | Summary: This paper proposes GENIE, a novel stochastic optimizer designed for Domain Generalization (DG) tasks. Unlike standard optimizers (SGD, Adam, etc.) that can over-emphasize certain “spurious” features, GENIE uses a metric called One-Step Generalization Ratio (OSGR) to guide parameter updates. The key idea is to balance the contribution of each model parameter to the on-step generalization ability, thereby preventing a small subset of parameters from dominating the learning.
GENIE introduces 3 main components in its update rule: 1) a preconditioning factor per parameter to equalize OSGR contributions, 2) a noise injection term to encourage exploration of flatter minima, and 3) a dropout mask on gradients to reduce overfitting and stabilize updates. By incorporating these, GENIE aims to promote domain-invariant features learning and avoid reliance on domain-specific correlations.
The authors show theoretically that GENIE achieves a higher OSGR than conventional optimizers while retaining the same convergence rate as SGD. Empirically, GENIE consistently outperforms baseline optimizers like SGD, Adam, Yogi, AdaBelief, AdaHessian, and SAM on average accuracy across several standard DG benchmarks (PACS, VLCS, OfficeHome, TerraIncognita, DomainNet) following DomainBed protocols.
Overall, the paper’s conceptual contribution is introducing OSGD-guided optimization to balance gradient contributions, and its main finding is that this leads to more robust models that generalize better to unseen domains.
Claims And Evidence: Some claims stated in the paper are as follows:
a. Standard optimizers allow a few parameters to dominate updates.
b. The proposed GENIE optimizer increases OSGR and leads to better domain generalization performance than existing optimizers.
c. GENIE maintains the convergence speed of SGD despite its modifications.
d. Integrating GENIE with known DG methods yields additional improvements without altering those methods’ architectures.
e. Uniformly distributed OSGR across parameters indicates better generalization.
Overall, claims a – d are substantiated by either theoretical derivations or thorough experiments. Claim e, however, is not explicitly proven. This is stated as a conjecture rather than a theorem, and while intuitively supported (and aligned with their results), it’s not rigorously demonstrated beyond the heuristic argument.
Additionally, the authors claim that GENIE “naturally” leads to flatter minima despite not explicitly optimizing sharpness. While this is plausible, the paper doesn’t directly measure curvature or sharpness of minima, so this particular point remains a bit informal argument.
Methods And Evaluation Criteria: The proposed methods are well-aligned with the DG problem setting. GENIE’s optimizer design is appropriate because it directly tackles a known challenge in DG: avoiding overfitting to source-specific features by modulating how each parameter learns.
The approach is conceptually sound – using preconditioning to scale parameter-wise gradients based on their signal-to-noise ratio (GSNR) ensures that no parameter with high variance or spurious signal gets overly large updates. This is analogous to adaptive optimizers like Adam adjusting for gradient variance, but here it’s done with a generalization-focused objective.
Introducing noise injection and a random mask (dropout) on gradients is also sensible for DG. These add stochasticity and regularization to escape narrow minima and reduce reliance on any single feature.
The evaluation criteria and settings are appropriate and rigorous. The authors adhere to the standard DomainBed evaluation protocol, which is a well-accepted framework for DG comparisons. Furthermore, baselines include both generic optimizers (SGD, Adam variants, SAM) and DG-tailored optimizers like FAD and GAM, as well as DG algorithms like IRM, CORAL, RSC integrated with standard optimizers. This comprehensive evaluation is appropriate for demonstrating GENIE’s effectiveness.
The only slight critique in methodology is the treatment of statistical significance and variability. The paper reports mean accuracies but does not mention standard deviations or confidence intervals. DG results can have high variance across training runs, so typically multiple runs are averaged. It’s not explicitly stated if results are averaged over several trials or a single run (though DomainBed usually averages over 3 seeds). Aside from that, the chosen benchmarks, baselines, and protocols are the gold standard for this problem, making the valuation criteria appropriate and convincing.
Theoretical Claims: The paper provides theoretical analysis to support GENIE’s design, including proofs and derivations in Appendix. I think that the main theoretical contributions are Corollary 3.2, Corollary 3.3, and Theorem 3.9.
Corollary 3.2 modifies the original OSGR formulation from Liu et al. 2020 (Theorem 3.1) by adding a per-parameter preconditioner. By setting $p_j = \frac{1}{E[g_j^2],(r_j + 1/n)}$, it equalizes each parameter’s influence. Corollary 3.3 shows that GENIE’s OSGR is higher than or equal to that of SGD and ADAM. Theorem 3.9 addresses convergence, stating that under standard assumptions (bounded gradients, Lipschitz smoothness, non-zero gradient noise), the average gradient norm under GENIE’s updates decays on the order $O(T^{-1/2})$.
Overall, the theoretical claims seem sound, and I did not find any obvious errors in the proofs. It is important to note that the assertion “uniform OSGR leads to better generalization” is presented as a conjecture—it guides the algorithm design but is not rigorously proven. This is acceptable as a motivational idea rather than a strict claim.
Experimental Designs Or Analyses: The experimental design is comprehensive and well thought-out. The authors run experiments on multiple datasets (5 benchmarks) and settings to cover different aspects of domain generalization. On average, GENIE is empirically proven to provide better generalization than other optimizers (Tables 2 and 3).
The ablation on the PACS dataset (Table 6) is sound, systematically toggles Preconditioning, Noise, and Mask components. The results show that Preconditioning alone yields most of the gain.
The experimental design could be further strengthened by reporting variability (e.g., results over 3 independent runs as DomainBed usually does). It appears they might have used fewer hyperparameters tuning trials than DomainBed defaults due to computational limits, but I could not find any report if each result is an average of multiple runs or a single best run.
Supplementary Material: I reviewed almost all parts of supplementary materials, particularly contents showing the theoretical proofs.
Relation To Broader Scientific Literature: The paper’s contributions fit well into the evolution of DG methods: early work focused on invariances and domain adversarial training (MTAE, DANN), then came gradient-based regularization (IRM, VREx, RSC), and now we see optimization-level interventions (SAM, FAD, GENIE). In my opinion, the idea of using one-step generalization ability as a guiding principes is novel in DG.
OSGR as a metric came from prior work, but applying it to actively adjust training (as an optimizer) is a fresh contribution that pushes the literature toward thinking about “how” the model learns, not just “what” it learns.
Essential References Not Discussed: I did not find major omissions of essential references.
Other Strengths And Weaknesses: Strengths
Originality: The paper takes a fresh approach by introducing a new optimizer specifically for domain generalization. Optimizer-level solutions in DG are still relatively rare, so GENIE offers a fresh perspective.
Significance: The empirical gains, while moderate on average (~2-3% over strong baselines), are consistent and achieved on challenging benchmarks. Hitting a new state-of-the-art on DomainBed’s suite (with a simple plug-in optimizer) is significant for the DG community. Moreover, the method’s success in single-domain generalization (which many algorithms can’t handle) is a notable achievement – it suggests GENIE is capturing something fundamental about robust learning. If these results hold, GENIE could become a go-to optimizer for any training models for unknown target domains.
Weaknesses
Complexity and Practicality: One potential weakness is the added complexity of the optimizer. GENIE introduces several hyperparameters (preconditioning factors via momentum/variance decay, noise scale, dropout probability) and requires tracking second moment estimates per parameter (like Adam). Practitioners might need to tune the noise scale or dropout probability for different tasks.
Lack of Direct Analysis or Feature Invariance: The paper claims GENIE promotes domain-invariant features, but it doesn’t directly evaluate this claim by examining feature representations. For example, some DG papers use metrics like center divergence between domain features or visualization of learned features.
Other Comments Or Suggestions: Typos and Wording:
- optionaly --> optionally
- randam mask --> random mask
- what’s meant by “... enough for suppress enough ...” at P8?
Questions For Authors: 1. Did you run multiple trials with different random seeds for training, and if so, how consistent were the results for GENIE and other optimizers?
2. Could you clarify how hyperparameter search was done for GENIE vs other baselines?
3. The noise injection uses a factor $1 - \tanh(1/\sigma^2_t)$ to scale Gaussian noise. Why was this specific form chosen?
4. What dropout probability $p$ do you use for the random mask on gradients? Is it the same across all experiments (and all layers/parameters)? And did you need to tune this probability?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your detailed and constructive review.
# A1
As you pointed out, our initial submission reported only the best single trial due to computational constraints. Following your suggestion, we have now conducted additional experiments with three independent trials per optimizer using random seeds {0, 1, 2}, and report the mean accuracy and 95% confidence intervals below. GENIE consistently outperforms the baselines across datasets with low variance. The full set of results will be included in the appendix of the final version.
|PACS|Art|Cartoon|Photo|Sketch|Avg|
|----|---|-------|-----|------|----|
|Adam|88.0±1.2|79.7±0.5|96.7±0.4|72.7±0.9|84.3|
|SGD|85.1±0.4|76.0±0.3|98.3±0.4|60.3±6.1|79.9|
|SAM|85.7±1.2|81.0±1.4|97.1±0.2|77.4±1.8|85.3|
|GENIE(our)|88.7±0.7|82.8±1.3|98.5±0.1|81.3±0.4|**87.8**|
|VLCS|Caltech|LabelMe|SUN|VOC|Avg|
|----|-------|--------|---|---|----|
|Adam|98.9±0.4|65.9±1.5|71.0±1.6|74.5±2.0|77.3|
|SGD|98.4±0.2|64.7±0.7|72.5±0.8|76.6±0.8|78.1|
|SAM|98.5±1.0|66.2±1.6|72.0±1.0|76.1±1.0|78.2|
|GENIE(our)|99.3±0.3|67.2±1.5|76.6±0.3|79.7±0.8|**80.7**|
|OfficeHome|Art|Clipart|Product|Real-World|Avg|
|----------|---|-------|-------|-----------|----|
|Adam|63.9±0.8|48.1±0.6|77.0±0.9|81.8±1.6|67.6|
|SGD|65.3±0.8|48.8±1.4|76.7±0.3|83.0±0.7|68.5|
|SAM|63.5±1.2|48.6±0.9|77.0±0.8|82.9±1.3|68.0|
|GENIE(our)|66.2±0.5|55.0±0.4|77.5±0.4|80.0±0.5|**69.7**|
|TerraInc|L100|L38|L43|L46|Avg|
|--------------|----|---|---|---|----|
|Adam|42.2±3.4|40.7±1.2|59.9±0.2|35.0±2.8|44.4|
|SGD|41.8±5.8|39.8±3.9|60.5±2.2|37.5±1.1|44.9|
|SAM|42.9±3.5|43.0±2.2|60.5±1.6|36.4±1.2|45.7|
|GENIE(our)|55.2±4.8|47.5±2.1|59.2±0.4|45.9±1.0|**52.0**|
# A2
For baseline optimizers, we used results from Zhang et al. (ICCV 2023) obtained under the DomainBed framework. For GENIE, two hyperparameters—dropout probability $p$ and the moving average coefficient $\beta$—were tuned via the standard DomainBed hyperparameter selection procedure (hparams_seed ∈ {0, ..., 19}), selecting configurations with the highest validation accuracy. We further discuss hyperparameter sensitivity in our response to **Reviewer V3wF (A2)**, and will publicly release optimized hyperparameters for reproducibility.
# A3
The preconditioning value includes the term $\tanh(1/\sigma_t^2)$, which tends to suppress the updates of gradients with high variance. While this helps avoid overfitting to noisy gradients, it can undesirably reduce updates to certain parameters. To counterbalance this suppression, we introduce a reciprocal noise scaling factor $1 - \tanh(1/\sigma_t^2)$ which amplifies the noise component where variance is high, encouraging exploration of alternative solutions. This form was chosen to maintain a complementary relationship with the preconditioning factor and encourage escape from sharp or suboptimal minima.
# A4
We treated the dropout probability $p$ as a global hyperparameter, applying it uniformly across all layers and parameters for simplicity and consistency. This hyperparameter was tuned individually for each dataset.
---
While not explicitly raised as formal questions, we would also like to respectfully address several concerns implied in your review:
# Feature Invariance
You correctly noted the lack of feature-level analysis supporting our claim of domain-invariant features. To address this, we have now included t-SNE and UMAP visualizations (fully anonymized): [**URL**](https://imgur.com/a/Pu3xrOi). These results clearly demonstrate improved cross-domain feature alignment and support our claims about domain-invariant feature learning.
# OSGR Conjecture
We agree that the conjecture about uniform OSGR leading to better generalization lacked formal proof. However, Section 3.3.1 shows analytically that our proposed preconditioning yields more uniform parameter-wise OSGR, thereby achieving higher total OSGR across all parameters as implied by Jensen's inequality. Additionally, Liu et al. (ICLR 2020) established that higher total OSGR correlates with improved generalization. We recognize that this point is a critical part of our contribution. To further address this concern, we refer to our response to **Reviewer MLrB**, which includes a PAC-Bayesian analysis comparing GENIE with SAM, showing our method explicitly minimizes the KL term for better generalization.
# Sharpness
We acknowledge your point that we claimed GENIE naturally leads to flatter minima without explicitly measuring curvature. While the SAM method is grounded in PAC-Bayesian theory and focuses on sharpness—which can be interpreted as a bound on empirical risk with respect to the posterior parameter distribution—we would like to highlight that, Our preconditioning strategy provide an additional benefit: it also contributes to tightening the generalization bound by explicitly minimizing the KL divergence term as our answer to **Reviewer MLrB**.
We hope our clarifications adequately address your concerns and demonstrate the rigor and value of our proposed method.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for all my concerns and recommend accepting the paper for the conference. Please include all additional insights discussed in the rebuttal to the final manuscript.
---
Reply to Comment 1.1.1:
Comment: Thank you for your positive feedback and constructive comments! We appreciate your recommendation for acceptance, and we will incorporate all the additional insights discussed in the rebuttal into the final manuscript to further improve the work. | Summary: This paper proposes a novel optimizer that leverages the one-step generalization ratio to assess each parameter’s contribution to loss reduction, aiming to promote domain-invariant feature learning.
Claims And Evidence: The paper’s claims are clearly stated, and the experiments presented provide convincing evidence in support of these claims.
Methods And Evaluation Criteria: Both the proposed method and the chosen evaluation metrics align well with the stated research problem.
Theoretical Claims: I’ve checked the proofs and no issues are found.
Experimental Designs Or Analyses: The experimental setup is generally solid. However, to further validate the effectiveness of the proposed optimizer, I recommend extending the experiments to segmentation or detection tasks in domain generalization settings (e.g., from GTAV to Cityscapes, BDD100K, and Mapillary). In addition, exploring how different hyperparameters (such as β1 and β2) influence the optimizer’s performance would provide valuable insights into its sensitivity to hyperparameter choices.
Supplementary Material: The appendix contains proofs, pseudo-code, and additional experiments, which sufficiently support the main text.
Relation To Broader Scientific Literature: The paper references and conducts experiments on domain generalization tasks and includes comparisons with other existing optimizers.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None.
Questions For Authors: Please address my concerns raised under “Experimental Designs or Analyses.”
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments. Below, we address the points raised under "Experimental Designs or Analyses":
# A1
Because of limited time and computational resources, we were unable to include experiments on additional tasks such as object detection or segmentation within the submission period. We fully agree that evaluating GENIE on a wider range of tasks (e.g., detection, segmentation, or face anti-spoofing) would further validate its generalization capabilities. We consider this an important direction for future work and plan to release additional results and code for these tasks moving forward.
# A2
GENIE uses two key hyperparameters: the dropout probability $p$ and a moving average coefficient $\beta$ (used for computing the running mean and variance of gradients). We conducted an additional hyperparameter sensitivity analysis on the OfficeHome dataset to examine the impact of these parameters. As shown by our new experimental results, GENIE consistently outperforms SGD, Adam, and SAM across a range of $p$ and $\beta$ values, demonstrating the method’s robustness to these hyperparameters. (All other training settings were held constant in this analysis.)
We note that we performed a grid search to tune hyperparameters in this new experiment; in contrast, for all other experiments we followed the DomainBed protocol and selected hyperparameters based on validation performance. We hope these clarifications address your concerns. Thank you again for your thoughtful and constructive feedback.
see: [**URL**](https://imgur.com/a/puvgaCx). (The link is fully anonymized.)
---
We hope these clarifications address your concerns. Thank you again for your thoughtful and constructive feedback. | null | null | null | null | null | null | null | null |
The Emperor's New Clothes in Benchmarking? A Rigorous Examination of Mitigation Strategies for LLM Benchmark Data Contamination | Accept (poster) | Summary: This paper discusses a way to evaluate Benchmark Data Contamination (BDC) mitigation strategies. The authors set up two key standards, Fidelity and Contamination Resistance, as criteria of assessing reliability of each method. By following a rigorous evaluation pipeline, experiments on 10 LLMs, 5 benchmarks, and 20 BDC mitigation strategies show that no existing strategy significantly improves resistance over the vanilla "no benchmark update".
Claims And Evidence: Yes, the authors set up a robust evaluation framework and provided relevant results to support their claim.
Methods And Evaluation Criteria: Yes, the authors provided an intuitive evaluation framework.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes, the experimental design is clear. But there are some concerns regarding the soundness. Please refer to Weaknesses and Questions below.
Supplementary Material: Yes, I've checked the experimental results that support the method choices.
Relation To Broader Scientific Literature: This work points out the weaknesses of prior BDC mitigation strategies, and calls for further research with respect to the criteria provided by the authors.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: ## Strengths
- The idea is intuitive and the experimental pipeline is robust.
- The paper reads well and is well organized
## Weaknesses
- I am not sure why high Fidelity is desired. The goal of BDC mitigation strategies is to deviate from the original benchmark, which is potentially utilized during LLM pre-training. The updated benchmark differing from the original version is not itself a problem, as long as the benchmark is evaluated on fairly. The authors did provide an example of "turning GSM8K into a history-based benchmark" in L181, but this is an excessively extreme case to justify using Fidelity as a criterion.
- If Contamination Resistance is intended to consider the advantage of using the original benchmark in fine-tuning, why not just exclude the ratio of "incorrect -> correct"? I am not sure why "correct -> incorrect" should also be excluded in the resistance ratio.
- While the overall evaluation pipeline is solid, one other concern is in the fundamental problem of the contamination detection task. The task of contamination detection itself is very difficult and is hard to verify the validity. Even if the authors used three detection methods to filter benchmarks, the following experiments building on this can be seen as unreliable.
- In summary, based on my concerns, I am not certain if the paper's claim is sound. (1) Benchmark selection is questionable, and (2) the evaluation criteria needs further justification. Thus, the claim that none of the prior work meeting reliability standards is rather misleading.
Other Comments Or Suggestions: N/A - see Strengths and Weaknesses
Questions For Authors: N/A - see Strengths and Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Q1: Why high fidelity is necessary
High fidelity is necessary because a low fidelity score indicates that the updated benchmark has undergone **excessive** changes from the original benchmark, which can introduce two practical issues:
(1) **Answer invalidation**: The modifications may alter the semantics of a question such that the original answer is no longer correct, requiring human annotation to ensure correctness.
(2) **Difficulty or objective drift**: The updated question may no longer be appropriate for LLM evaluation. It could become too difficult, too trivial, or deviate the focus to unintended skills or knowledge domains. This requires human annotators not only to provide a new answer but also to assess whether the question remains suitable for evaluation.
We provide qualitative examples of these two cases in Tables 6 and 5, respectively. Both issues contradict the goal of BDC mitigation strategies, which is to **automatically and efficiently** update benchmarks without requiring manual checks. High fidelity ensures that updated benchmarks remain aligned with the original evaluation objective and usable at scale.
If our goal is to derive a *new* benchmark and then evaluate all models fairly (as you might have in mind), a high fidelity is not required. However, in this case, human annotation and evaluation for the validity of the new benchmark is often required, and it is a different setting from BDC contamination.
> Q2: Why exclude "correct->incorrect" in contamination resistance
The goal of a mitigation strategy is to enable accurate measurement of a model’s true capability, even if the model has been **contaminated by the original benchmark**. Contamination resistance is therefore designed to assess whether the **updated benchmark** can preserve this measurement.
If we include "correct->incorrect" cases, we may encourage scenarios where the clean model outperforms the contaminated model on the updated benchmark, i.e., $R(M,D^S) > R(M^D,D^S)$. In practice, this would lead to **underestimating** the model’s true capacity and contradict the goal of mitigation, which is to recover reliable evaluation even after contamination. This is why **symmetric matching** is essential in our definition.
> Q3: Benchmark selection is questionable
we have made our **best effort** to filter contamination by applying three BDC detection methods from distinct categories and selecting only models regarded as uncontaminated by all three on all benchmarks. However, we acknowledge that we still cannot fully rule out the possibility of contamination.
That said, we have made every effort to select benchmarks to ensure reliable conclusions. The four benchmarks we use, GSM8K, MMLU, Arc-C, and TruthfulQA, are **widely adopted** in prior BDC mitigation work [1-4]. In addition, we include the RepliQA dataset, a recently released benchmark with non-factual, fictional contexts. Its **recent release and non-factual nature** make it highly unlikely to be present in any model’s training data, making it a suitable candidate in our controlled pipeline.
> Q4: Refining the claim to avoid misinterpretation
To prevent misunderstanding, we will revise the abstract and introduction to more precisely state our claim:
(1) While some *semantic-preserving* mitigation strategies (e.g., MPA and ITD) achieve significantly higher resistance scores than the vanilla case on **certain benchmarks** (e.g., MMLU, TruthfulQA, and RepliQA), no strategy consistently outperforms the vanilla case **across all benchmarks** in a **statistically significant** manner.
(2) Further, although some strategies perform well on one metric, none effectively balances both fidelity and contamination resistance.
-------
[1] Clean-eval: Clean evaluation on contaminated large language models
[2] Inference-time decontamination: Reusing leaked benchmarks for large language model evaluation
[3] Automating dataset updates towards reliable and timely evaluation of large language models
[4] Dynamic Evaluation of Large Language Models by Meta Probing Agents
---
Rebuttal Comment 1.1:
Comment: Thank you for the responses. I believe Q1 is an important aspect that requires detailed discussion in the paper. I suggest the authors include a section dedicated to relevant discussions in the final version.
Other concerns are mostly addressed - I adjusted the score accordingly.
Thank you.
---
Reply to Comment 1.1.1:
Comment: Thank you for taking the time to reevaluate our work and for your thoughtful feedback! We agree that Q1 raises an important point regarding the necessity of high fidelity, and we will include a comprehensive discussion in the final version to highlight its motivation and implications.
If you have any further questions or suggestions, please feel free to let us know—we strive to consistently improve the quality and clarity of our paper. | Summary: Designed a systematic and controlled pipeline to provide fine-grained and comprehensive assessment of existing benchmark data contamination mitigation strategies. They focus on a question-level study experimenting with 10 LLMs, 5 benchmarks, 20 mitagation stagetries with 2 scenarios. From this, they find that no existing strategy significantly impacts benchmark resutls.
Claims And Evidence: Claim that existing BDC mitigation strategies are not sufficient, introducing fidelity and contamination resistance metrics. They provide evidence of this in section 3 and 5.
Methods And Evaluation Criteria: The paper evaluates the mitigation strategies through their two interpretable scores: Fidelity and Resistance.
Theoretical Claims: n/a
Experimental Designs Or Analyses: The experimental design is solid. The only issue might be the number of LLMs evaluated.
Supplementary Material: skimmed the appendix
Relation To Broader Scientific Literature: This is a good overview of existing mitigating techniques in previous literature and rigirously evaluating them.
Essential References Not Discussed: Might want to include the following citations in the related work: [1] "To the cutoff... and beyond? a longitudinal perspective on LLM data contamination" https://openreview.net/forum?id=m2NVG4Htxs, [2] "Bring Your Own Data! Self-Sensitivity Evaluation for Large Language Models" https://openreview.net/forum?id=k2xZYPZo34#discussion, and "Training on the test task confounds evaluation and emergence" https://openreview.net/forum?id=jOmk0uS1hl
[1] studies data contamination through the lens of time.
[2] proposes a new evaluation framework for mitigating contamination.
[3] shows that training on the test task can improve performance.
Other Strengths And Weaknesses: Strengths:
- Interesting finding
- Good experimental design
Weaknesses:
- More datasets (i.e adding code evals) and models
Other Comments Or Suggestions: For table 3, can you reconstruct this table in the appendix with an added row by weight class (including the number of models in that weight class)? I wonder if the size of the model impacts these scores. I wonder if the conclusions might be different under this view.
Questions For Authors: See comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > W1: More datasets and models
Our current study includes 10 LLMs, 5 benchmarks, 20 mitigation strategies, and 2 contamination scenarios, yielding 10×5×20×2 = 2000 evaluation results. While we believe this already provides a comprehensive analysis, we agree that including more models and benchmarks would further strengthen the reliability of our findings. We will discuss this as a limitation and explore broader coverage in future work.
> Q1: Model size vs. resistance scores
This is an excellent question. We appreciate the suggestion and will include an extended version of Table 3 in the appendix with model size weight information.
Inspired by this question, we explore the correlation between model size and contamination resistance. We examine two perspectives: **raw resistance scores** and **resistance improvement over the vanilla baseline**. Our key finding is that **(1) larger models generally exhibit higher raw resistance scores, but (2) their relative advantages over mitigation strategies tend to diminish with scale**, as detailed below.
(1) For each semantic-preserving mitigation strategy, we compute the average resistance score across all datasets and calculate its Spearman correlation with model size. **All strategies show positive correlations with model size.** This indicates even after being exposed to the original benchmark, larger models tend to preserve their evaluations on the updated benchmark, indicating higher behavioral stability.
|Strategy|Corr (raw resistance) |Corr (resistance improvement)|
|-|-|-|
|Back-translation|0.33|-0.72|
|Clean-Eval|0.40|-0.31|
|Additional Incorrect Choices|0.69|-0.80|
|Irrelevant Context|0.31|-0.70|
|ITD|0.23|-0.31|
|MPA|0.29|-0.14|
|MPA-Choice + Trans-CN|0.64|-0.63|
|MPA-Ques + Trans-CN|0.53|-0.14|
|Choice Paraphrasing|0.68|-0.60|
|Choices Permutation|0.68|-0.79|
|Relevant Context|0.37|-0.36|
|Synonym Replacement|0.33|-0.12|
|Syntactic Modification|0.31|-0.49|
|Translation (Chinese)|0.65|-0.14|
|Translation (French)|0.61|0.05|
|Typographical Perturbation|0.32|-0.39|
|Vanilla|0.45|/|
(2) However, as discussed in Section 5.1, contamination resistance should be interpreted **relative to the vanilla baseline**. To assess this, we computed the correlation between model size and the resistance improvement (i.e., the difference between the strategy's resistance and that of the vanilla baseline; averaged across all datasets). **Under this view, the correlations are mostly negative**. This indicates that the *relative effectiveness* of current mitigation strategies diminishes for larger models. It highlights the need for more robust and scalable approaches that can adapt to larger LLMs.
> Additional reference
Thank you for the suggestions. We will include the listed citations in the related work section for completeness.
---
Rebuttal Comment 1.1:
Comment: Can you show me raw values for model size vs resistance scores like Table 3? You can group Strategies by type or just select a couple strageries, but please include Paraphrasing as one of them.
---
Reply to Comment 1.1.1:
Comment: We provide below the raw resistance scores under both **mild** and **intensive** contamination for the vanilla case and four semantic-preserving strategies: **Synonym Replacement**, **Syntactic Modification**, **Choice Paraphrasing** (as requested), and **MPA**. Rows correspond to LLMs, and columns correspond to benchmarks.
|Model|Arc-C|MMLU|TruthfulQA|GSM8K|RepliQA|
|-|-|-|-|-|-|
||Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|
|Llama-3.2-3B|0.904/0.870|0.873/0.833|0.728/0.643|0.694/0.688|0.871/0.803|
|Yi-1.5-6B|0.890/0.553|0.866/0.791|0.749/0.625|0.735/0.718|0.724/0.455|
|vicuna-7B|0.862/0.797|0.858/0.825|0.668/0.431|0.541/0.408|0.837/0.661|
|Llama-3.1-8B|0.885/0.837|0.821/0.766|0.748/0.624|0.735/0.755|0.444/0.209|
|Falcon3-10B|0.965/0.952|0.934/0.923|0.796/0.693|0.817/0.820|0.932/0.923|
|Qwen2.5-14B|0.962/0.952|0.935/0.907|0.892/0.794|0.815/0.819|0.679/0.581|
|Phi-3-medium|0.945/0.936|0.888/0.858|0.902/0.837|0.828/0.848|0.900/0.833|
|DeepSeek-V2-Lite|0.906/0.910|0.901/0.902|0.734/0.605|0.726/0.716|0.909/0.845|
|Qwen2.5-32B|0.977/0.974|0.929/0.921|0.909/0.859|0.789/0.795|0.632/0.592|
|Yi-1.5-34B|0.932/0.918|0.812/0.797|0.814/0.755|0.797/0.799|0.161/0.071|
**Table 1: Vanilla**
|Model|Arc-C|MMLU|TruthfulQA|GSM8K|RepliQA|
|-|-|-|-|-|-|
||Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|
|Llama-3.2-3B|0.899/0.877|0.887/0.845|0.716/0.610|0.704/0.695|0.896/0.854|
|Yi-1.5-6B|0.889/0.846|0.876/0.820|0.738/0.622|0.691/0.716|0.809/0.609|
|vicuna-7B|0.869/0.809|0.860/0.805|0.672/0.447|0.620/0.491|0.869/0.757|
|Llama-3.1-8B|0.901/0.846|0.830/0.774|0.748/0.605|0.725/0.757|0.539/0.341|
|Falcon3-10B|0.957/0.956|0.944/0.929|0.786/0.683|0.813/0.810|0.952/0.939|
|Qwen2.5-14B|0.957/0.949|0.936/0.908|0.890/0.788|0.815/0.816|0.762/0.712|
|Phi-3-medium|0.943/0.931|0.913/0.877|0.909/0.860|0.828/0.832|0.917/0.869|
|DeepSeek-V2-Lite|0.905/0.908|0.884/0.905|0.743/0.594|0.732/0.726|0.916/0.894|
|Qwen2.5-32B|0.980/0.980|0.929/0.921|0.922/0.868|0.777/0.782|0.776/0.750|
|Yi-1.5-34B|0.938/0.922|0.821/0.806|0.813/0.727|0.778/0.791|0.291/0.159|
**Table 2: Synonym Replacement**
|Model|Arc-C|MMLU|TruthfulQA|GSM8K|RepliQA|
|-|-|-|-|-|-|
||Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|
|Llama-3.2-3B|0.899/0.871|0.859/0.817|0.717/0.628|0.708/0.709|0.902/0.880|
|Yi-1.5-6B|0.870/0.822|0.860/0.813|0.760/0.644|0.714/0.712|0.792/0.588|
|vicuna-7B|0.886/0.817|0.871/0.838|0.657/0.459|0.640/0.543|0.873/0.749|
|Llama-3.1-8B|0.891/0.849|0.841/0.775|0.756/0.641|0.710/0.747|0.506/0.320|
|Falcon3-10B|0.950/0.936|0.944/0.944|0.796/0.677|0.801/0.794|0.939/0.938|
|Qwen2.5-14B|0.952/0.950|0.924/0.896|0.879/0.797|0.812/0.824|0.784/0.729|
|Phi-3-medium|0.937/0.928|0.894/0.869|0.889/0.835|0.817/0.829|0.906/0.863|
|DeepSeek-V2-Lite|0.901/0.904|0.878/0.895|0.731/0.602|0.721/0.724|0.921/0.897|
|Qwen2.5-32B|0.980/0.977|0.926/0.922|0.919/0.875|0.794/0.801|0.821/0.784|
|Yi-1.5-34B|0.930/0.917|0.822/0.808|0.810/0.743|0.781/0.785|0.311/0.146|
**Table 3: Syntactic Modification**
|Model|Arc-C|MMLU|TruthfulQA|
|-|-|-|-|
||Mild/Intensive|Mild/Intensive|Mild/Intensive|
|Llama-3.2-3B|0.900/0.892|0.863/0.832|0.726/0.633|
|Yi-1.5-6B|0.894/0.817|0.849/0.824|0.761/0.627|
|vicuna-7B|0.882/0.832|0.860/0.839|0.685/0.449|
|Llama-3.1-8B|0.893/0.848|0.835/0.776|0.770/0.654|
|Falcon3-10B|0.951/0.955|0.930/0.928|0.797/0.698|
|Qwen2.5-14B|0.956/0.955|0.937/0.907|0.880/0.800|
|Phi-3-medium|0.933/0.941|0.891/0.875|0.908/0.857|
|DeepSeek-V2-Lite|0.896/0.904|0.894/0.902|0.737/0.608|
|Qwen2.5-32B|0.978/0.980|0.928/0.927|0.897/0.870|
|Yi-1.5-34B|0.928/0.914|0.850/0.817|0.810/0.726|
**Table 4: Choice Paraphrasing (only 3 multiple-choice benchmarks available)**
|Model|Arc-C|MMLU|TruthfulQA|GSM8K|RepliQA|
|-|-|-|-|-|-|
||Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|Mild/Intensive|
|Llama-3.2-3B|0.890/0.876|0.842/0.810|0.759/0.665|0.733/0.735|0.924/0.900|
|Yi-1.5-6B|0.888/0.783|0.873/0.855|0.798/0.633|0.738/0.731|0.902/0.799|
|vicuna-7B|0.902/0.887|0.892/0.889|0.733/0.540|0.719/0.681|0.897/0.845|
|Llama-3.1-8B|0.887/0.879|0.865/0.813|0.825/0.652|0.686/0.705|0.732/0.538|
|Falcon3-10B|0.953/0.960|0.926/0.931|0.852/0.766|0.845/0.832|0.940/0.940|
|Qwen2.5-14B|0.944/0.954|0.924/0.930|0.884/0.853|0.810/0.816|0.875/0.854|
|Phi-3-medium|0.962/0.966|0.930/0.921|0.931/0.860|0.863/0.865|0.938/0.922|
|DeepSeek-V2-Lite|0.901/0.922|0.911/0.919|0.810/0.693|0.733/0.727|0.933/0.906|
|Qwen2.5-32B|0.963/0.973|0.952/0.941|0.924/0.882|0.754/0.770|0.892/0.885|
|Yi-1.5-34B|0.916/0.919|0.894/0.881|0.823/0.707|0.741/0.750|0.673/0.442|
**Table 5: MPA**
**Due to space limitations, we only present a subset of strategies here. If there are additional strategies you are interested in, please feel free to let us know—we would be glad to provide the corresponding results or include them in the final appendix.** | Summary: This paper introduces a systematic pipeline and proposes two metrics—fidelity and contamination resistance—to provide a fine-grained and comprehensive assessment of existing benchmark data contamination (BDC) mitigation strategies. The authors evaluated 20 different BDC mitigation approaches across 10 LLMs, 5 benchmarks, and 2 contamination scenarios, and found that none of the existing mitigation strategies consistently improved contamination resistance across all benchmarks while maintaining fidelity to the original tests
Claims And Evidence: There are some contradictory claims, for instance:
a. The authors mention that no existing BDC mitigation strategy is effective. However, the results show that some strategies (e.g., MPA, ITD, and Analysis Extension) significantly outperform the vanilla (no mitigation) approach
b. The paper assumes that existing benchmarks (e.g., MMLU, GSM8K) are high-quality but there are already updated versions of these benchmarks due to issues like wrong labels, data contamination, etc. [1, 2].
1. Zhang, Hugh, et al. "A careful examination of large language model performance on grade school arithmetic." Advances in Neural Information Processing Systems 37 (2024): 46819-46836.
2. Wang, Yubo, et al. "Mmlu-pro: A more robust and challenging multi-task language understanding benchmark." The Thirty-eight Conference on Neural Information Processing Systems Datasets and Benchmarks Track. 2024.
Methods And Evaluation Criteria: 1. While the proposed methods and evaluation criteria are not something groundbreaking (i.e., instead of applying approaches like paraphrasing, fine-tuning, etc.), they still make sense.
2. The authors also fail to justify the novelty of their proposed metrics.
Theoretical Claims: 1. No issues.
Experimental Designs Or Analyses: Contamination scenarios are quite synthetic, making the generalizability of the results questionable.
Supplementary Material: Yes. Discussion, Related work, Pipeline.
Relation To Broader Scientific Literature: 1. Contamination scenarios are quite synthetic, making the generalizability of the results questionable.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: Strength:
1. Studied a very important topic.
Weaknesses:
1. Wrong claims, lacking substantial contributions,
Other Comments Or Suggestions: N/A
Questions For Authors: a. Why did you mention that no existing BDC mitigation strategy is effective even though your experiment shows contradictory results?
b. Why did you state that existing benchmarks (e.g., MMLU, GSM8K) are high-quality but there are already updated versions of these benchmarks due to issues like wrong labels, data contamination, etc.
c. What is the technical novelty of the proposed metrics?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: > W1 & Q1: Misunderstanding of contradictory results
We clarify that our claim is not contradictory: while some **semantic-preserving** mitigation strategies (e.g., MPA and ITD) achieve significantly higher resistance scores than the vanilla case on **certain benchmarks** (e.g., MMLU, TruthfulQA, and RepliQA), no strategy consistently outperforms the vanilla case **across all benchmarks** in a **statistically significant** manner (Table 3). Our conclusion excludes semantic-altering strategies (e.g., Analysis Extension), which are only applicable to Arc-C and MMLU and thus insufficient to support a general claim.
To prevent misunderstanding, we will revise the abstract and introduction to make the claim more accurate.
> Q2: Justifying the use of existing benchmarks in BDC mitigation evaluation
We emphasize that BDC mitigation is an established line of research [1–4], which builds on the assumption that widely used benchmarks such as MMLU and GSM8K are high-quality and representative of real-world question distributions. These benchmarks are commonly adopted in prior work proposing mitigation strategies to address contamination. **Building upon their assumptions**, our paper rigorously examines the effectiveness of such strategies.
High quality does not imply perfection. Rather, it suggests that these benchmarks have broad coverage aligned with the intended evaluation objectives, making them worth preserving through mitigation rather than replacement. While we acknowledge that benchmarks like MMLU and GSM8K may contain incorrect labels and suffer from data contamination, even **their revised versions** (e.g., MMLU-Pro, GSM1K) **remain vulnerable to contamination**. This further motivates the need for robust contamination mitigation strategies and careful evaluation of their effectiveness.
We thank the reviewer for highlighting this point and the relevant references, and will cite them and include a discussion in the revision.
> Q3: Novelty of the proposed metrics
We identify clear limitations in existing practices for assessing BDC mitigation strategies: (1) Accuracy drop **ignores clean accuracy**, making it unclear how much drop reflects effective mitigation; (2) Accuracy matching focuses on aggregate accuracy but **overlooks question-level mismatches**. For example, a strategy with high accuracy matching may still alter the original benchmark’s evaluation objective (Fig 2(b)).
Motivated by these issues, we propose two metrics, fidelity and contamination resistance, that explicitly capture **two** types of **question-level alignment** using normalized Hamming distance. To our knowledge, this is the first work to examine BDC mitigation effectiveness along these two orthogonal dimensions, covering more desirable aspects of mitigation strategies and enabling finer-grained analysis than prior approaches.
> Experimental Designs Or Analysis: On the realism of contamination scenarios
We included two contamination settings in our paper that reflect **common and established** practices in prior BDC mitigation work: (a) Intensive Contamination [1,3]: fine-tuning the LLM with only benchmark data. (b) Mild Contamination [4]: fine-tuning on benchmark data mixed with 20K instruction-following samples from OpenOrca.
Motivated by your concern, we **add experiments** on two more scenarios: (c) Partial Contamination: only **half of the benchmark** is included in fine-tuning, mixed with 20K OpenOrca samples, while evaluation is done on the **entire benchmark**. This reflects situations where only a portion of the evaluation data is seen during training. (d) Indirect Contamination: fine-tuning and evaluation use different splits of the same benchmark, again mixed with 20K OpenOrca samples. This setting captures contamination via exposure to data from the same distribution during training, without direct sample overlap with evaluation data.
We experiment with 8 LLMs and 2 datasets, evaluating all 16 semantic-preserving strategies. We report only those strategies (with resistance scores) that achieve **statistically significantly higher resistance than Vanilla**; full results will be included in the revised appendix.
(1) Partial contamination:
- Arc-C: No strategy shows significant improvement over Vanilla;
- TruthfulQA: Back Translation (0.807), ITD (0.824), MPA (0.833), and MPA-Ques + Trans-CN (0.813) outperform Vanilla (0.795).
(2) Indirect contamination:
- Arc-C: No strategy shows significant improvement over Vanilla;
- TruthfulQA: ITD (0.821), MPA (0.839), and MPA-Ques + Trans-CN (0.815) outperform Vanilla (0.791).
These empirical results echo with our main claim (refer to W1 & Q1).
---
[1] Clean-eval: Clean evaluation on contaminated large language models
[2] Dynamic evaluation of large language models by meta probing agents
[3] Automating dataset updates towards reliable and timely evaluation of large language models
[4] ConStat: Performance-Based Contamination Detection in Large Language Models | Summary: This paper investigates mitigation strategies for benchmark data contamination (BDC) in LLM evaluation. The authors argue that current approaches for assessing BDC mitigation strategies, which focus on aggregate accuracy metrics, have significant limitations. To address this, they propose two metrics---fidelity and contamination resistance---that enable question-level evaluation. Experiments with 10 LLMs, 5 benchmarks, and 20 mitigations strategies show that no existing strategy consistently outperforms the vanilla approach (i.e. no dataset update) across all benchmarks, and none balances both fidelity and contamination resistance.
Claims And Evidence: The claims are generally well-supported by evidence. The authors claim that previous BDC mitigation assessment methods are insufficient is argued through examples in Figure 2, and show why question-level matching is more informative than aggregate accuracy.
The central claim that no existing strategy significantly improves resistance over the vanilla case across all benchmarks is supported by the results in Tables 3 and 4, with statistical significance testing. The data shows that while some strategies perform well on specific benchmarks, none consistently outperforms across all datasets.
The claim regarding the trade-off between fidelity and resistance is also shown in Figure 4, where strategies are visibly clustered in either high-fidelity/low-resistance or low-fidelity/high-resistance regions, with none achieving both high fidelity and high resistance.
Methods And Evaluation Criteria: The methodology is appropriate and includes uncontaminated LLM-benchmark pair selection using three BDC detection methods, application of 20 mitigation strategies, controlled contamination under two scenarios (mild and intensive), and evaluation using the proposed metrics.
The selection of benchmarks (Arc-Challenge, MMLU, TruthfulQA, GSM8K, and RepliQA) and models (10 LLMs ranging from 3B to 34B parameters) provides good coverage of different evaluation contexts.
Theoretical Claims: The paper focuses on empirical evaluation and makes limited formal theoretical claims. The definitions of fidelity and contamination resistance in Section 3 are mathematically sound, as is the extension to continuous evaluation scores in Appendix A.1.
Experimental Designs Or Analyses: The experimental design is well-constructed with appropriate controls like three BDC detection methods to ensure uncontaminated baseline models, two different contamination scenarios, validation of contamination effectiveness, and monitoring model perplexity on held out data. One potential limitation is the focus on a specific finetuning approach for contamination.
Supplementary Material: Reviewed parts of the supplementary material on the extension of the evaluation framework to continuous scores, related work on BDC detection, and implementation details. The examples of mitigation strategies are particularly helpful for understanding how each strategy transforms the benchmark samples.
Relation To Broader Scientific Literature: The paper is well-situated within the broader literature on LLM evaluation and benchmark contamination. The authors acknowledge two primary approaches to addressing BDC: creating new benchmarks and updating existing ones, focusing on the latter as a more cost-effective approach. They build upon previous mitigation strategies like Clean-Eval, ITD, and MPA while addressing limitations in their evaluation methodologies. The discussion of BDC detection methods is comprehensive, categorizing them into token probability-based, generation-based, and order-based approaches.
Essential References Not Discussed: Recent work on red-teaming LLMs and adversarial robustness provide some insights on developing perturbation techniques that maintain semantic equivalence while bypassing pattern recognition. These approaches directly relate to the semantic-preserving strategies examined in the paper.
Other Strengths And Weaknesses: Other weaknesses:
- The benchmarks and experiments used are primarily multiple-choice and more straightforward open-ended questions, so it is unclear whether the findings generalizes to more complex evaluation tasks.
- While the experiments cover 10 LLMs, they are all relatively small (3B to 34B parameters) compared to the SOTA models, which raises questions about if and how the results generalizes to larger models.
Other Comments Or Suggestions: It would be interesting to see some discussion probablistic evaluation metrics that account for uncertainty in model responses are alternatives to the binary evaluation vectors used in the paper's metrics and could potentially offer a more nuanced assessment of contamination effects.
Questions For Authors: 1. Have you noticed any patterns in the types of questions that benefit most from specific mitigation strategies?
2. Any ideas for mitigation strategies that would more effectively balance fidelity and resistance?
3. Have you explored/observed any correlation between the model size and their susceptibility to contamination and the responsiveness to mitigation strategies?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > W1: More complex evaluation tasks
Thank you for the insightful suggestion. As the first work to rigorously assess BDC mitigation strategies for LLMs, we focus on commonly used evaluation tasks as adopted in prior BDC mitigation studies [1-3]. We agree that extending the analysis to more complex evaluation tasks is an important direction. We will discuss this limitation in the revised paper and explore it in future work.
> W2: Larger LLMs
We agree that including larger models would further strengthen the reliability of our findings. However, our setup adopts **full fine-tuning** because it more faithfully approximates real-world contamination scenarios, where models are exposed to benchmark data during pre-training or continued training, compared to parameter-efficient methods like LoRA. However, full fine-tuning can be computationally expensive for larger LLMs.
Notably, most prior works on BDC mitigation [1-2] only consider LLMs with up to 13B parameters. In comparison, our study includes models up to 34B, and we have made every effort to scale as far as our resources allow. We plan to include larger models in future work as resources permit.
> S1: Discussion of probabilistic evaluation metrics
Thank you for the valuable perspective. We will include a discussion of this point in the revised paper and consider it as part of future work.
> Q1: Any patterns in the types of questions that benefit most?
For multiple-choice benchmarks, we find that ITD, MPA, and choice permutation achieve high contamination resistance. In contrast, for open-ended benchmarks, we do not observe any strategy that consistently and statistically significantly outperforms the vanilla baseline in terms of contamination resistance. This may be due to the greater variability and flexibility of open-ended responses, which makes stable mitigation more difficult.
> Q2: Toward strategies that better balance fidelity and resistance
One potential direction we are exploring in separate work involves training two reward models, one for fidelity and one for resistance, and using them to jointly guide the LLM in conditionally updating benchmarks that score highly on both axes. This remains an open question without a definitive solution, and we believe learning-based approaches offer a potential path forward.
> Q3: Correlation between model size and (1) susceptibility to contamination and (2) responsiveness to mitigation
This is an excellent question. (1) Inspired by it, we compute the Spearman correlation between model size and accuracy inflation (averaged across 5 datasets) under mild and intensive contamination. We observe a negative correlation, suggesting that larger models exhibit less accuracy inflation under contamination. One possible explanation is that their stronger generalization capabilities make them less dependent on memorized benchmark content.
|Contamination|Corr (**averaged** across 5 datasets)|
|-|-|
|Mild|-0.018|
|Intensive|-0.401|
(2) We further explore the correlation between model size and contamination resistance. Specifically, for each semantic-preserving mitigation strategy, we compute the average resistance score across all datasets and calculate its Spearman correlation with model size. **All strategies show positive correlations with model size.** This indicates even after being exposed to the original benchmark, larger models tend to preserve their evaluations on the updated benchmark, indicating higher behavioral stability.
|Strategy|Corr (raw resistance) |Corr (resistance improvement)|
|-|-|-|
|Back-translation|0.33|-0.72|
|Clean-Eval|0.40|-0.31|
|Additional Incorrect Choices|0.69|-0.80|
|Irrelevant Context|0.31|-0.70|
|ITD|0.23|-0.31|
|MPA|0.29|-0.14|
|MPA-Choice + Trans-CN|0.64|-0.63|
|MPA-Ques + Trans-CN|0.53|-0.14|
|Choice Paraphrasing|0.68|-0.60|
|Choices Permutation|0.68|-0.79|
|Relevant Context|0.37|-0.36|
|Synonym Replacement|0.33|-0.12|
|Syntactic Modification|0.31|-0.49|
|Translation (Chinese)|0.65|-0.14|
|Translation (French)|0.61|0.05|
|Typographical Perturbation|0.32|-0.39|
|Vanilla|0.45|/|
However, as discussed in Section 5.1, contamination resistance should be interpreted **relative to the vanilla baseline**. To assess this, we computed the correlation between model size and the resistance improvement (i.e., the difference between the strategy's resistance and that of the vanilla baseline; averaged across all datasets). Under this view, **the correlations are mostly negative**. This indicates that the *relative effectiveness* of current mitigation strategies diminishes for larger models. It highlights the need for more robust and scalable approaches that can adapt to larger LLMs.
---
[1] Clean-eval: Clean evaluation on contaminated large language models
[2] Automating dataset updates towards reliable and timely evaluation of large language models
[3] Dynamic Evaluation of Large Language Models by Meta Probing Agents | null | null | null | null | null | null |
Optimizing Test-Time Compute via Meta Reinforcement Finetuning | Accept (poster) | Summary: The paper formalizes the problem of optimizing test-time compute as a meta-reinforcement learning problem and proposes to use cumulative regret as an optimizing objective instead of barely the outcome reward. The cumulative regret can be calculated by estimating the information gain. The authors further develop the meta-reinforcement finetuning (MRT) and show that MRT leads to substantial improvement on the AIME dataset.
## update after rebuttal
The authors have addressed my concerns and I will keep my score of 4 and suggest for acceptance.
Claims And Evidence: The claims are generally supported by the experimental evidence in the paper.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense.
Theoretical Claims: N. A.
Experimental Designs Or Analyses: I checked all experimental designs and analyses. They look good to me. For additional comments, please refer to Other Strengths And Weaknesses.
Supplementary Material: I have reviewed the supplementary materials. Some of the experimental details are missing and I recommend the authors adding more experimental details in the appendix.
Relation To Broader Scientific Literature: How to optimize the model to efficiently use additional test-time compute is a very important problem since the release of OpenAI-o1 model. The authors analyze the open-sourced reasoning model from a novel meta-RL perspective and propose new method that show significant improvement, which contributes to the development of more advanced reasoning model.
Essential References Not Discussed: It's probably good to at least mention OpenAI O1 model and cite their blog post.
Other Strengths And Weaknesses: The paper is generally well-written with interesting idea of formulating the test-time computing problem as a meta-RL problem. The idea and the proposed approach are both interesting and novel. The results are also solid. However, I find some of the writings confusing and can be further improved. Please see below for additional weaknesses.
1. In Fig. 2 of the analyses of Deepseek-R1, the authors mix pass@k, majority@p and the episodes together, which makes this plot rather confusing at first glance. Also, I do not know how the authors make the plot for accuracy versus log-tokens. I would assume that different problems would have very different number of tokens per episode/pass. Those details are not clear even after reading the relevant appendices.
2. The papers lack some details regarding how they perform the experiments. I suggest the authors adding the experimental details to the appendix. For example, the authors suggest that one can either use another LLM or the same LLM as the policy model to estimate the information gain. However, which LLM is used and how it is used to estimate the information gain is not clear from the paper for the experiments conducted.
3. It is a little confusing for RL to run for multiple iterations since the authors use an online-RL framework. I guess the authors mean running with additional randomly sampled subset of the dataset. I suggest the authors clarifying this confusion.
Other Comments Or Suggestions: Typos: repeated learning rate in table 1.
Questions For Authors: 1. In Fig. 6 and Fig. 7, the curves of MRT-B end earlier in number of tokens. Would it be helpful to steer the model to continue the episodes? Would it continuously improve the performance as reported in the s1 paper or would it saturate instead?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive review of the paper! We will add more experimental details to the Appendix – in particular, regarding the experimental setting for both MRT (STaR), MRT (RL), and analysis on R1, and we will also cite the [o1](https://openai.com/o1/) and [o3](https://openai.com/index/openai-o3-mini/) blog post in the paper. We will address your concerns below, and would appreciate it if you would be willing to raise your score if you find your concerns addressed. We are happy to answer any remaining questions.
> In Fig. 2 of the analyses of Deepseek-R1, the authors mix pass@k, majority@p and the episodes together, which makes this plot rather confusing at first glance. Also, I do not know how the authors make the plot for accuracy versus log-tokens. I would assume that different problems would have very different number of tokens per episode/pass. Those details are not clear even after reading the relevant appendices.
It's correct that different problems would have very different numbers of tokens per episode and different numbers of episodes. Therefore, we first split the problems into different groups based on the number of episodes. For all solutions with a certain number of episodes (e.g., 6-10, 26-30), we average the number of tokens per episode and accuracy across those solutions. In other words, to plot the blue line, we fix j, find the average number of tokens up to j episodes, and then average maj@k given j episodes in the thought block across different solutions. Please let us know if this is clear, and we will add this discussion to the paper as well.
> The authors suggest that one can either use another LLM or the same LLM as the policy model to estimate the information gain. However, which LLM is used and how it is used to estimate the information gain is not clear from the paper for the experiments conducted.
Thanks for the question! We will use the one extra page in the final version to also include more details in the main paper and definitely add the rest to the appendix.
In regards to your question above, we note that there are multiple ways to estimate the information gain or rewards. In this paper, we use Monte Carlo rollouts with the base model as the estimator. Specifically, to compute the reward of a given prefix, we sample multiple rollouts to complete this prefix with the base model. We then use the success rate among these rollouts to represent the reward of the prefix. The reason we mention that "one can either use another LLM or the same LLM as the policy model to estimate the information gain" is because Monte Carlo rollouts are not the only method to estimate rewards. One can also train a progress reward model to assess how effective a prefix is for a given problem, or use an LLM as a judge to provide the estimation.
> It is a little confusing for RL to run for multiple iterations since the authors use an online-RL framework. I guess the authors mean running with additional randomly sampled subset of the dataset. I suggest the authors clarifying this confusion.
Yes, and multiple iterations are also useful to update the reference model to prevent it from being too different / off-policy.
> Would it be helpful to steer the model to continue the episodes with MRT? Would it continuously improve the performance as reported in the s1 paper or would it saturate instead?
**New results in more open-ended settings:**
To extend MRT to more episodes, we ran MRT directly on top of distilled variants of DeepSeek-R1. We refer to this setting as the "open-ended" setting, since the episodes now – much like our analysis in Section 4 – are not constrained to follow a specific format. We defer the training details to the [supplement](https://sites.google.com/view/icml25mrt/home#h.hx11wcth8wc3). We evaluated MRT and GRPO on AIME 2024/25, and AMC 2023 datasets (20 samples per problem) from different base models in the [supplement](https://sites.google.com/view/icml25mrt/home#h.d85qg8xhjc12). Our models fine-tuned on DeepScaleR-1.5B-Preview achieve state-of-the-art performance for their size: **47.2% success on AIME 2024 and 39.7% on AIME 2025**. Across multiple base models, MRT's relative performance improvement is about **2–3x** compared to outcome-reward RL (GRPO).
We also measure the cumulative regret metric for both MRT and other baselines (STaR, GRPO, base model). To do so, we first run the R1 analysis on our own models and take the optimal policy $\pi^*$ to be the one that achieves perfect accuracy in one episode. Intuitively, we are computing the red area (denoting cumulative regret) normalized at different cutoff points/token budgets. As shown in the [supplement](https://sites.google.com/view/icml25mrt/home#h.nllm3x1c80pa), models trained with MRT have the lowest regret. Moreover, in extrapolation regions where we steer our trained model to think more with "Wait" (similar to S1), the performance of **MRT doesn't plateau but continues to improve**.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their responses to my questions. Including additional experimental details in the paper is important for clarity and understanding. The quality of the paper would be significantly improved if these details were incorporated. I have no further concerns and recommend that the paper be accepted.
---
Reply to Comment 1.1.1:
Comment: Thank you for your thoughtful feedback. We're glad that we've addressed all your concerns and appreciate your recommendation for acceptance! We will certainly incorporate all the additional experimental details into the final version of the paper as suggested.
Since our revisions have addressed your concerns and will improve the paper's quality, we respectfully ask if you might consider raising your evaluation score to reflect these improvements. And thank you again for your valuable input throughout this review process. | Summary: This paper introduces Meta Reinforcement Finetuning (MRT), a framework to optimize how large language models (LLMs) utilize test-time computational resources. The authors frame test-time compute optimization as a meta reinforcement learning (RL) problem, where the LLM generates a stream of token episodes (e.g., reasoning steps, backtracking attempts) to solve a query. The goal is to minimize cumulative regret, a metric measuring how effectively intermediate episodes contribute to discovering the correct answer. MRT augments standard outcome-based RL (e.g., 0/1 correctness) with a dense reward bonus based on the information gain from each episode. This reward quantifies the utility of intermediate steps in reducing uncertainty about the final answer. The results demonstrate that optimizing for cumulative regret via MRT enables LLMs to balance exploration and exploitation, improving both efficiency and generalization to larger test-time budgets. The framework is scalable and adaptable to diverse reasoning strategies beyond backtracking.
Claims And Evidence: **MRT-B Improves Efficiency and Performance**
Combing MRT-B with STaR and GRPO, experiments on AIME show 30% and 38% token efficiency gains over baselines (Figures 7–8). However, in Figure 10, the information gain bonus underperforms length-penalized RL in reducing the completion length. Actually, the length does not decrease compared with GRPO at all on the right side of Figure 10. Why the length is not decreased? Didn't MRT increase token efficiency?
Besides, although the paper's analyze seems suitable for multiple episodes, but in the pseudocode in Appendix B, the experiments are only on z_0, z_{1:2}, only two episodes? It might be a drawback of this paper if I understand this correctly.
**Existing Methods (e.g., DeepSeek-R1) Exhibit High Regret**
Section 4 demonstrates that DeepSeek-R1’s accuracy plateaus or degrades with more episodes Figures 2. The figure is a little bit hard to understand, I will say my understanding and you can say if it is correct. The 6 dots on the "direct" line are pass@k=1,2,4,8,16,32. You break the reasoning at step 0,5,10,15,20... to compute maj@p, p=1,2,8. But I see three green dots in each green line, so I assume it should be p=1,2,4,8? There is no green line breaching from early episode since at early episode p>1 is the same as p=1. So your result is basically saying that the in later episodes, it is better to do parallel sampling than sequential sampling.
Besides, I checked Appendix C, The Omni-MATH subset (40 problems) and AIME (30 problems) are small and may not reflect broader generalization.
Methods And Evaluation Criteria: **Information Gain Calculation**
In definition 5.1, to calculate the information gain, it requires to sample repeatedly at the end of episodes, will that be the major computational cost in the training?
**Equation (2)**
The introduction of information gain into the rl is interesting. But how is $c_k$ generated? what is the relationship between $z_1, z_2\cdots, z_{k-1}$, they are independently generated by pi conditioned on $c_k$? And how is $k$ defined here?
**Warmstart SFT’s**
In Sec 6.2, this paper proposed to construct a warmstart dataset. I think the desription of the construction is not clear. Using Figure 5 as an example, using what metric (in math equation) you choose node 2, from node 2, can we construct something like 0-2-6-13-5-9-14-5-9-15, i.e., two wrong answer before one correct ones. Besides, why your construction is easy to fit, is it because of common prefix of correct and wrong answer? If the prefix was shared more, such as 0-2-6-11-17-16, will this be easier to fit?
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: See previous reviews.
Supplementary Material: Yes. I review the Appendix B and C. The description of the experiments is detailed.
Relation To Broader Scientific Literature: N.A.
Essential References Not Discussed: The references are properly discussed.
Other Strengths And Weaknesses: See previous reviews.
Other Comments Or Suggestions: See previous reviews.
Questions For Authors: This paper proposes an interesting method in test-time-compute, but some writings of the methods can be improved. I am willing to raise my score if my concerns are resolved.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your feedback! To address your concerns, we clarify the notion of token efficiency and interpret the results of MRT in comparison with length-penalty and baseline GRPO, add new results running MRT on top of DeepSeek-R1 models to extend beyond three-episode setting, and add numerous visualizations of regret with and without MRT to justify the efficacy of the regret metric. **Please let us know if your concerns are addressed, and if so, we would be grateful if you could raise your score.**
> [New expt.] Results for multiple episodes
To extend MRT to more episodes, we ran MRT directly on top of distilled variants of DeepSeek-R1. This “open-ended setting” removes the constraints on the episodes to follow a specific format, making them freeform similar to our analysis in Section 4. We defer the training details to the [supplement](https://sites.google.com/view/icml25mrt/home#h.hx11wcth8wc3).
**Results:** We evaluated MRT and GRPO on AIME 2024/25, and AMC 2023 datasets from different base models in [supplement](https://sites.google.com/view/icml25mrt/home#h.d85qg8xhjc12). Our models fine-tuned on DeepScaleR-1.5B-Preview achieve state-of-the-art performance for their size: **47.2% success on AIME 2024 and 39.7% on AIME 2025**. Across multiple base models, MRT's relative performance improvement is about **2–3x** compared to outcome-reward RL (GRPO).
**Comparisons to length penalty:** We also run an additional comparison on top of the DeepScaleR-1.5B model, where we apply an explicit length penalty but fine-tune it with GRPO. In agreement with findings in the submission, we find that incorporating a length penalty results in worse pass@1 accuracy.
In the [supplement](https://sites.google.com/view/icml25mrt/home#h.39szyztelvn4), we also measure the cumulative regret of MRT, GRPO/STaR, and base models. To do so, we choose $\pi^*$ to be the one that achieves perfect accuracy within one episode. Intuitively, we are computing the red area in the [supplement](https://sites.google.com/view/icml25mrt/home#h.ytlrapcrku0y) normalized for different token budgets. MRT attains smallest regret, even when extrapolating beyond training budget (similar to [s1](https://arxiv.org/abs/2501.19393)).
> Token efficiency and length penalty
To clarify, **token efficiency refers to maximum performance at minimal tokens.** The tradeoff of using length penalty is that although it reduces the number of tokens substantially, the performance plateaus beyond a point (e.g., see Figure 10, when tokens > 8000). MRT surpasses it when we allow a larger number of tokens, and the model's performance continues to increase. In addition, note that in the above experiments, MRT even outperforms length penalty in terms of pass@1 performance.
> Computation cost of MRT
In supplement, we compute the total FLOPs used by MRT and STaR/GRPO for sampling and training. For NuminaMATH (20,000 problems) with Llama-3.1-8B-Instruct, STaR required 2.62×10²⁰ FLOPs while MRT needed 2.64×10²⁰ FLOPs (1.01× more) while attaining 1.7× fewer inference tokens. Similarly, GRPO used 6.34×10¹⁹ FLOPs versus MRT's 6.86×10¹⁹ FLOPs (1.08× more) but MRT used 1.6× fewer inference tokens. MRT uses <8% more computation while requiring 60% fewer tokens during inference to achieve the same performance.
> Understanding of Figure 4
Yes, your understanding is correct. To add to your point, this result is saying that sequential sampling does not realize the full potential of tokens spent, as the naive strategy of parallel sampling (maj@k) outperforms sequential thinking. When in principle, sequential thinking should easily express maj@k with the same number of tokens.
> How is $c_k$ generated?
Sorry for the confusion, it should be $c_j$, which consists of the prefix (first j episodes) sampled from the previous checkpoint. $k$ is defined as the number of episodes of the rollout. To avoid confusion, we provide a more detailed explanation of update in the [supplement](https://sites.google.com/view/icml25mrt/home#h.3d34xjyebemx).
> Sec 6.2, warmstart dataset construction and other construction schema.
In Figure 5, for each node from 0-13, we compute the information gain by using Definition 5.1, and select the one that maximizes the information gain. And yes, we can construct in other formats as suggested. Motivated by this, we extend the method to an open-ended setting.
> Besides, I checked Appendix C, The Omni-MATH subset (40 problems) and AIME (30 problems) are small and may not reflect broader generalization.
As shown in the [supplement](https://sites.google.com/view/icml25mrt/home#h.sej9e58f36gr), we added more results by evaluating Deepseek-R1 on AIME problems from 2015-2024 (293 problems in total). Our findings from the submission still hold, where the performance of off-the-shelf models does not improve as the thinking budget increases, and simple early termination with parallel sampling outperforms, but the model couldn't discover such solution.
---
Rebuttal Comment 1.1:
Comment: Thanks for providing additional experiments. I have changed my score to 4.
---
Reply to Comment 1.1.1:
Comment: Thank you for your valuable feedback. We’re glad that we’ve addressed all your concerns and greatly appreciate your recommendation for acceptance. As suggested, we’ll ensure that all the additional experimental details are incorporated into the final manuscript. | Summary: This paper suggests a novel perspective on test time compute through long generation through the formulation of meta-rl. It suggests that the correct way to trade exploration and exploitation, in this case, is through the notion of cumulative regret. Furthermore, it claims that we should judge if a partial response (=an episode) contributed to the overall success of the trajectory through a notion of information gain. The information gain can be used as an additional reward term, which leads to the MRT algorithm - a variant of either STaR or GRPO with the additional reward bonus. The method is evaluated on mathematical reasoning tasks (NuminaMATH and AIME datasets) and shows improved accuracy and token efficiency compared to standard outcome-reward RL.
Claims And Evidence: In Figure 8, it seems like the difference between GRPO (Iter 2) and MRT (Iter 2) is only 1-2%. Can you please provide numerical values with CI so we will be able to understand if the gains are actually statistically significant?
Methods And Evaluation Criteria: Equation 2 is not written in a clear way - does c_k contain k or j episodes?
It also doesn’t align with the description of the MRT-B (RL) algorithm. There, You use \pi_old as \mu, to get an estimation of the information gain of z_0. This is unlike equation 2, where \pi_old is used to sample context. Please clarify it.
Theoretical Claims: - Line 261 claims that “[utilizing previous policy] allows us to improve over the previous policy provably” but doesn’t provide proof.
- You introduce a reward bonus term to the RL problem, as defined in equation 2. Will the optimal policy for the augmented reward is the same as for the original one? I think this is an important thing to clarify.
Experimental Designs Or Analyses: Figure 2 confuses me. First, when you calculate maj@p for DeepSeek-R1. Do you sample the episodes p times or just the final response provided by \mu p times? If the latter, why does maj@p appears in the plot, as it contains multiple episodes? I understand why it is plotted as requiring more tokens but not more episodes.
In addition, my understanding is that maj@p is just a way to get a better estimation of the regret by constructing a more accurate \mu. If this is indeed the idea, why compare accuracy? Why the y axis in Figure 2 is not regret?
In general, the paper pushes the use of cumulative regret as a metric but doesn’t include any plot or other quantitive results that use it as a metric. This is one of the things that bother me the most.
Supplementary Material: I've read the supplementary materials and have no questions.
Relation To Broader Scientific Literature: The paper mentions STaR multiple times without ever explaining the algorithm. I think spending a few lines explaining it (maybe in section 2?) will make the paper easier to read for people who are not well-versed in the literature.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: I think the perspective of test-time computing as a meta-rl problem is novel and interesting to the community. In addition, the reward shaping term suggested in the paper is grounded and seems helpful to the training process.
In addition, the paper provides a significant amount of experiments, checking the reward term on top of two popular algorithms - STaR and GRPO.
There are two main reasons I currently tend to reject the paper: the fact that the proposed metric is not used in either the analysis of current algorithms or the evaluation of the new one. And the fact that I'm not sure how significant the gain from MRT is compared to the baselines.
Other Comments Or Suggestions: In Figure 4, it says once that J_r(\mu(\cdot|z_1,z_0,x) equals 0.5 and the other time it equals 0.75, and the third time that it is 0.25. Is it a typo?
Questions For Authors: MRT-B requires running meta-prover rollouts to estimate information gain, adding significant computational overhead to the training. For large-scale tasks or bigger models, it could become expensive to run repeated queries at intermediate steps. The paper would benefit from a more thorough discussion of how costly this is.
Both versions of MRT were trained to improve only the first rollout (z_0). Do you think extending the algorithm to evaluate the information gain of z_2, z_4,… will result in even bigger gains? I understand that such runs can be computationally expensive, therefore I’m not necessary expect numerical results.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback! We've added new results measuring regret for MRT and baselines, showing MRT attains smaller regret and improved performance in more general settings. We will also update the paper with more clarifications and the definition of STaR. **If your concerns are addressed, we'd be grateful if you could raise your score.**
> Significance of maj@k results in Figure 2 and measuring regret
**Motivation for measuring maj@k.** Our goal with maj@k is not to compute regret, but to demonstrate a simple baseline using partial thinking traces that outperforms sequential thinking with more episodes. If sequential thinking worked effectively, it should have outperformed this basic maj@k approach (blue >> green).
**Regret measurements:** We initially didn't measure regret because, similar to RL, this requires comparison against an optimal policy π* that's unknown beforehand. Performance over more episodes served as our proxy. However, we can consider the optimal comparator π* to be the one that achieves perfect accuracy in one episode. Here, the regret is the area between the blue / green / orange lines in Figure 2 and the horizontal line at y = 1. For each point on the R1 scaling curve, we can plot corresponding regret, normalized by episodes or tokens used. As shown in the [supplement](https://sites.google.com/view/icml25mrt/home#h.nllm3x1c80pa), the regret of direct and [maj@k]_j are lower compared to [maj@1]_j on solutions with more episodes, indicating that sequential episodes do not use tokens efficiently compared to majority voting from an earlier episode or the direct model.
> Performance gain over baselines from MRT
We want to highlight that the metric is not just pass@1 performance, but also token efficiency. We redrew the plots in the [supplement](https://sites.google.com/view/icml25mrt/home#h.ex6mhnuz4w7y) by omitting iter1 and highlighting token efficiency. With linearized evaluation, MRT achieves the same performance as GRPO with 1.6x fewer tokens.
**New results in more open-ended settings:** We extended MRT to distilled variants of DeepSeek-R1, where episodes aren't constrained to follow a specific format. We evaluated MRT and GRPO on AIME 2024/25, and AMC 2023 datasets (20 samples per problem) from different base models in [supplement](https://sites.google.com/view/icml25mrt/home#h.d85qg8xhjc12). Our models fine-tuned on DeepScaleR-1.5B-Preview achieve state-of-the-art performance for their size: **47.2% success on AIME 2024 and 39.7% on AIME 2025**. Across multiple base models, MRT's relative performance improvement is about **2–3x** compared to outcome-reward RL (GRPO).
The 95% confidence interval for our method fine-tuned from DeepScaleR-1.5B-Preview on AIME2024 is **±0.13%.** Given the stable estimation from 20 samples, we prioritized evaluating on more problems and omit the CI for other models.
> Computational overhead in MRT training.
As in [supplement](https://sites.google.com/view/icml25mrt/home#h.i3vh26dgt29u), we compute the total FLOPs used by MRT and STaR/GRPO for sampling and training. For NuminaMATH (20,000 problems) with Llama-3.1-8B-Instruct, STaR required 2.62×10²⁰ FLOPs while MRT needed 2.64×10²⁰ FLOPs (1.01× more) while attaining 1.7× fewer inference tokens. Similarly, GRPO used 6.34×10¹⁹ FLOPs versus MRT's 6.86×10¹⁹ FLOPs (1.08× more) but MRT used 1.6× fewer inference tokens. MRT uses <8% more computation while achieving same performance with 60% fewer tokens during inference.
> Equation 2 clarification
Thanks for pointing this out. It should be $c_{j}$, which consists of the prefix (first j episodes) sampled from the previous checkpoint $\pi_\text{old}$. We provide a more detailed explanation of updated equation 2 in the [supplement](https://sites.google.com/view/icml25mrt/home#h.3d34xjyebemx).
> clarify $\pi_\text{old}$ and $\mu$
Policy $\mu$ can be any LLM (e.g., an "-instruct" model which is told to utilize episodes so far to guess the best answer). For implementation simplicity we use the success rate of Monte-Carlo rollouts on $\pi_\text{old}$ to represent $\mu$. We will add this clarification to the paper.
> proof of claim in Line 26
The theoretical argument behind this line is from Section 3 of the [TRPO paper](https://arxiv.org/abs/1502.05477), which shows optimizing policy under the state distribution induced by the old policy with a KL-constraint on actions results in monotonic performance improvement.
> optimality of augmented reward
As shown in the [supplement](https://sites.google.com/view/icml25mrt/home#h.ytlrapcrku0y), the optimal policy for the augmented reward (Right, w/ information gain) will also attain maximal reward under the original reward (Left, w/o information gain). However, not every policy that achieves the highest original reward exhibits maximal information gain. To see this intuitively, note that Equation (1) only guarantees correctness of the outcome, whereas maximal information additionally does so quickly.
---
Rebuttal Comment 1.1:
Comment: Thank you to the authors for their response. Their clarification helped me better understand the proposed method, and the new results support their claims.
However, the empirical gains from the proposed method still appear marginal compared to GRPO, especially considering the added complexity of the training procedure.
I will update my score accordingly.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response and for increasing your score! We are glad that our clarifications helped in this case.
Regarding the bit that “the gains from the proposed method appear marginal compared to GRPO,” we would like to highlight several important considerations in regards to our results.
First, it’s worth noting that the base models in our new results were already trained with RL on potentially a larger superset of prompts, or distilled from RL-trained models. Given this initialization, we should expect the gains from any subsequent fine-tuning to be modest in absolute magnitude, due to (1) fine-tuning an already fine-tuned model which often is known to result in entropy collapse, and (2) we had to use this initialization due to a lack of compute for fine-tuning a base model from scratch. Despite this high starting point, MRT still demonstrates:
- Statistically significant and systematic gains with MRT that are 2-3× larger than those achieved by GRPO
- Approximately 1.7× improvement in token efficiency
- Less than 8% computation overhead from outcome-reward training
The primary aspect of MRT is to optimize dense rewards when using test-time compute. Concurrent work outside of optimizing test-time compute from the process reward model literature, [PAVs](https://arxiv.org/abs/2410.08146), also shows that dense rewards are more effective than outcome rewards, especially on hard problems (Figure 8b in https://arxiv.org/pdf/2410.08146) due to improved exploration. We hypothesize that this kind of a difference between using dense rewards in MRT vs outcome reward training via GRPO on hard problems will also carry over in our experiments, if given enough compute and training time, which we are in lack of due to limited computational power.
**New proposed experiment:** While we cannot run this experiment with dense rewards in time for the response since our compute for doing so was not available, we plan to run an experiment by re-running training with the DeepScaleR-1.5B recipe from scratch on their prompt mixture using dense rewards prescribed by MRT for the final (in contrast to fine-tuning the DeepScaleR-1.5B checkpoint). In addition, we will add a didactic experiment showing the efficacy of MRT on countdown (Game of 24) for the final version. | null | null | null | null | null | null | null | null |
LAST SToP for Modeling Asynchronous Time Series | Accept (poster) | Summary: The authors propose a method for modeling temporal event sequences by finetuning pretrained language models. The paper shows that by using a novel prompt tuning method they are able to outperform several baselines and ablations.
Claims And Evidence: On the whole, yes. I am generally skeptical of methods that adopt language models for time series forecasting, as prior work has shown that they are outperformed by simple linear methods \[1\]. However, the authors of this paper do compare to relevant TPP methods (Table 2), conduct strong ablations, and compare to a random baseline.
One other result from \[1\] is that randomly initialized language models (i.e. those without any pretraining at all) surprisingly perform just as well as pretrained models. The paper would be strengthened by showing that this is not the case for this task.
\[1\] Tan, Mingtian, Mike A. Merrill, Vinayak Gupta, Tim Althoff, and Thomas Hartvigsen. 2024. “Are Language Models Actually Useful for Time Series Forecasting?” arXiv. [http://arxiv.org/abs/2406.16964](http://arxiv.org/abs/2406.16964).
Methods And Evaluation Criteria: Yes, the evaluation methods and datasets are standard and appropriate.
Theoretical Claims: N/A
Experimental Designs Or Analyses: I have a few questions about the experiments that I've listed below. On the whole the experiments (including the "bonus" experiments in the appendix) are interesting and well thought out.
Supplementary Material: Yes, I read the Appendix.
Relation To Broader Scientific Literature: The contributions of this paper will be interesting to anyone working in the field of language models for time series, which is an active area of research. The StoP method is potentially of broad interest to the NLP community, although this is not the primary focus of the paper.
Essential References Not Discussed: See "Claims and Evidence"
Other Strengths And Weaknesses: The paper is very well written and contains exhaustive experiments.
Other Comments Or Suggestions: - No need to reintroduce the notation in lines 210-215, would help paper flow
- Your description of LoRA in Section 4.2 is confusing. My understanding is that you're simply applying the original technique, but the description reads as though you're making a novel contribution. This should be clarified.
Questions For Authors: - How does StoP compare to other prompt tuning techniques? It would appear that it is applicable to all kinds of NLP tasks, not just those involving time series. Your experiments show that it's really doing something different (and apparently better) than SP. Similarly, how do other techniques perform on this task?
- "For each of these datasets, the semantic meaning of the event type is unknown, and only the index of the event type is available." However, in Appendix A.4 you go on to to test the case where the event description is replaced with gibberish. This leaves me a little confused - in the main experiments (e.g. Table 1) does the model have access to semantic information about the events?
- If you tune LLMTime and LLMProcess rather than doing zero shot is the comparison still as favorable? I know that these models are originally proposed as zero-shot, but it seems like it would be a fairer comparison if you tuned them as well.
- Why are you using QLoRA rather than finetuning the whole model?
- How does your method compare to simpler, non-neural baselines?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's positive evaluation, thoughtful suggestions, and recognition of our contributions, including the LASTS representation and the Stochastic Soft Prompting (SToP) mechanism. We respond to each comment below:
**Random Initialization:** Thank you for highlighting this relevant literature. We evaluated pretraining on the Breakfast dataset's forecasting task and observed clear benefits: fine-tuning a randomly initialized model yielded F1-score 0.14 vs 0.26, Accuracy 0.21 vs 0.39, and MAE 39.29 vs 32.55. This highlights the value of text pretraining in our asynchronous setting, given the rich natural language input. We’re happy to include this as an additional baseline in the main table of the camera-ready version if the reviewer recommends it.
**Redundant Notation (Lines 210–215):** Thank you for pointing this out. We will remove the redundant notation.
**Clarification on LORA:** Our goal in this section was to show that LASTS integrates easily with existing PEFT methods like LoRA and Soft Prompting for adapting an LLM backbone. We acknowledge the wording may have caused confusion and will revise it to clarify that we use the original LoRA implementation from [1]
[1] https://github.com/huggingface/peft
**Questions**
1. We answer this in two parts:
- **SToP Generality:** We agree that SToP may have broader applicability, but the focus of our current work is specifically on asynchronous time series. Exploring SToP in other NLP domains is beyond the scope of this paper and is left for future work.
- **Comparison to Other Prompt Tuning Techniques:** We include the *most widely-used PEFT methods*—Soft Prompting and QLoRA—as strong representatives for LLM adaptation; please see our response to Reviewer L5nG titled "Comparison to Other Prompt-Based Adaptation Methods" for further details.
2. **Clarification on use of semantic information:** We appreciate the reviewer’s careful reading
- The three datasets in Table 1—Breakfast, MultiTHUMOS, and EPIC-KITCHENS—contain semantic information that is available to the model and used in our experiments. (L270-274)
- For the five TPP datasets shown in Table 2, event names are replaced by categorical indices, and neither our model nor any TPP baseline uses semantic information. (L264-267)
- The experiments in Appendix A.4 using gibberish and textual descriptions are controlled ablations designed to isolate the effect of semantic content.
These experiments demonstrate that our model is flexible and effectively utilizes semantic information when it is available. We will make this clarification more prominent in the camera version of the manuscript.
3. **Finetuning LLMTime, LLM Processes:** We focused on using these models in their zero-shot capacity, as they were specifically proposed and pretrained for that purpose. Since these methods are compared against LASTS in the same zero-shot setting, we believe our comparisons are fair and meaningful, especially to assess generalization without additional tuning. We also highlight this zero-shot comparison in our main paper (L381–384), Figure 5, and Appendix A.6. We agree that fine-tuning LLMTime and LLMProcesses could be interesting baselines, but it may require additional effort to determine the optimal fine-tuning recipe and ensure a fair evaluation between models. Therefore, we will consider it as part of our future work..
4. **QLoRA vs Full Finetune:** We chose QLoRA because it allows parameter-efficient adaptation with low memory cost, aligning with our goal of scalable deployment. As Table 1 and Appendix A.9 show, QLoRA performs competitively, and SToP improves upon it while using only 0.02% of model parameters. While full fine-tuning could potentially yield slightly improved performance, it would be computationally impractical given the limitations of our current hardware.
5. **Simpler non neural baselines:** We thank the reviewer for this suggestion. Our primary baselines were state-of-the-art TPP models and recent LLM/PEFT techniques. Most recent literature on asynchronous time series modeling has shifted toward neural approaches, and we follow this trend to maintain consistency with comparable works. In non-neural TPPs, the features and functional forms used to model event intensities, dependencies, and histories often need to be manually designed or based on assumptions. This restricts the model's ability to generalize to complex datasets. In contrast, neural models offer greater flexibility in modeling the intensity function, enabling them to capture intricate relationships within the data. This adaptability makes neural TPPs better suited to handle diverse and complex datasets, improving their generalization and performance.
Once again, thank you for your encouraging and constructive review. We are grateful for the thoughtful feedback. | Summary: This paper presents LASTS (Language-modeled Asynchronous Time Series), a novel framework for modeling asynchronous time series data using Large Language Models (LLMs). The approach addresses the challenges of irregular timing and diverse event types by representing asynchronous time series as natural language prompts, allowing LLMs to leverage their broad world knowledge for reasoning across different domains and tasks.
The authors introduce Stochastic Soft Prompting (StoP), a parameter-efficient adaptation technique that significantly improves model performance. Unlike traditional soft prompting, StoP randomly selects prefixes of the prompt during training, encouraging the learning of diverse representations and improving generalizability.
Through extensive experiments on real-world datasets, the paper demonstrates that LASTS achieves state-of-the-art performance across forecasting, anomaly detection, and data imputation tasks. The framework outperforms existing methods including temporal point process models, foundation models for time series, and other LLM-based approaches.
Claims And Evidence: Yes, I think most claims in the paper are well-supported.
1. LASTS effectively leverages LLMs for asynchronous time series analysis
This is supported by extensive experiments across multiple datasets and tasks (forecasting, anomaly detection, imputation) and demonstrated through comparisons with traditional temporal point process models and other LLM-based approaches.
2. Stochastic Soft Prompting (StoP) improves performance over traditional soft prompting
This is supported by quantitative results showing improvements in Macro-F1 scores across dataset and visualized through t-SNE projections demonstrating more diverse token representations in StoP.
3. LASTS is parameter-efficient
This is supported by implementation details showing only 1.6M trainable parameters for prompt tuning.
4. LASTS outperforms existing methods
This is supported by comprehensive comparisons with temporal point process models, foundation models for time series, and other LLM-based approaches.
Methods And Evaluation Criteria: Yes I do think they make sense for the problem studied.
For the LASTS framework, I think the approach of representing asynchronous time series as natural language prompts makes sense given the irregular timing and diverse event types characteristic of such data.
For the StoP technique, I think its modification to traditional soft prompting addresses the need for more diverse representations in prompt-based adaptation and the coarse-to-fine structure learned by StoP appears suitable for capturing both general task information and specific details in asynchronous time series.
Theoretical Claims: There are no theoretical claims in the paper.
Experimental Designs Or Analyses: I checked the soundess of the experimental designs and analyses of the paper. I think they are overall sound.
1. Experimental designs: The authors select diverse approaches as the baselines: including random baselines, foundation models for time series (Chronos), LLM-based approaches (LLMTime, LLMProcesses) and TPP models. The authors cover three text-based action datasets and five standard TTP datasets in the experiments. As for the evaluation metrics, the authors use M-F1, MAE and RMSE to evaluate the performance of models.
2. Analyses: The paper includes ablation studies comparing different prompt representations (time first vs. event first) and different time representations (inter-arrival times vs. durations). These analyses help establish the effectiveness of the chosen representations.
The comparison between StoP and traditional soft prompting is thorough, with both quantitative results and qualitative analysis of learned representations. The analysis of training speed differences between StoP and traditional soft prompting adds practical value. The evaluation of few-shot learning with varying numbers of examples (k=0 to k=10) is well-designed and provides useful insights into how many examples are needed for optimal performance. The identification of k=5 as the optimal few-shot setting is justified by the results.
Supplementary Material: No, I didn't.
Relation To Broader Scientific Literature: The paper's contributions represent meaningful advancements while building on established foundations in the field. The authors have successfully connected their work to prior literature, demonstrating how LASTS and StoP address limitations in existing approaches and extend the capabilities of LLMs to new types of data and tasks.
Essential References Not Discussed: No
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: None
Questions For Authors: 1. Did you perform chronological splitting of the datasets for train/validation/test, or was it done randomly? This is particularly important for time series data to avoid data leakage and better reflect real-world deployment scenarios. If random splitting was used, how might this affect the validity of your results compared to chronological splitting?
2. Beyond comparing with traditional soft prompting and QLoRA, have you considered comparing with other prompt-based adaptation methods like prefix tuning or adapter layers? How might these comparisons affect your claims about the superiority of StoP?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their thoughtful summary and generous assessment of our work. We are glad that the core contributions—LASTS and Stochastic Soft Prompting (SToP)—were found meaningful and well-supported. Below, we address the specific questions raised:
**Train/Validation/Test Splits**
We follow the standard protocol for each dataset as adopted in prior work (e.g., [Xue et al., 2024]). The splitting is done at the sequence level—given a dataset of N independent sequences, we use 80% for training, and 10% each for validation and testing, sampled independently from a shared distribution. The model thus learns patterns governing sequences of events and their interarrival times from the training set, and generalizes to unseen sequences in the validation and test sets. We use the standard protocol because it enables us to compare our results with those already published.
We acknowledge that traditional time series tasks require chronological splits to account for drift. However, in our datasets (e.g., EPIC-KITCHENS, MultiTHUMOS), the sequences are short, self-contained, and typically do not exhibit long-term temporal drift. This mitigates the need for chronological splitting. Nevertheless, we appreciate the reviewer’s concern and will make our data split methodology more explicit in the final version of the paper.
**Comparison to Other Prompt-Based Adaptation Methods**
Thank you for this suggestion. Many adapters have been proposed recently, and it would not be feasible to compare all of them. Therefore, we decided to focus our comparison on **widely-used PEFT techniques**: Soft Prompting and QLoRA. QLoRA is the standard adapter-based method and strong baseline, and we highlight that LASTS is compatible with such adapter techniques. Although we have not yet tried prefix tuning, there are no methodological limitations that would prevent its use with **stochastic training strategy (SToP)**, and we plan to investigate this in future work.
Once again, thank you for your encouraging and constructive review. We are grateful for the thoughtful feedback. | Summary: This paper introduces a novel framework for modeling asynchronous time series data using Large Language Models (LLMs). Unlike regular time series with evenly spaced time points, asynchronous time series consist of timestamped events occurring at irregular intervals, each described in natural language. This work demonstrates the potential of LLM-based approaches for asynchronous time series analysis across multiple tasks and domains, offering a flexible alternative to traditional methods while leveraging the world knowledge embedded in LLMs.
Claims And Evidence: 1. LASTS as an effective framework for asynchronous time series modeling
- Evidence: Comprehensive evaluations across multiple datasets (Breakfast, MultiTHUMOS, EPIC-KITCHENS and five standard TPP datasets) show consistent performance improvements.
- The zero-shot performance of LASTS exceeds other zero-shot baselines (Tables 1, 2, Figure 4).
- Comparison with specialized TPP models shows competitive or superior performance (Table 2).
2. Stochastic Soft Prompting (SToP) outperforms other PEFT methods
- Evidence: Detailed comparative results show SToP consistently outperforming SP and QLoRA across datasets and tasks (Table 1).
- Appendix Tables 6-7 quantify the performance gains (average 12.69% M-F1 improvement over SP and 13.55% over QLoRA).
- Training efficiency measurements show ~25% faster training than standard soft prompting.
3. Multi-task capability without task-specific designs
- Evidence: The same LASTS representation is successfully applied to forecasting, imputation, and anomaly detection without architectural changes (Table 1).
- Performance on all three tasks significantly exceeds baselines when using the adapted models.
4. Ability to handle large event spaces
- Evidence: Successful modeling of EPIC-KITCHENS dataset with ~20,000 unique event descriptions.
- Table 2 indicates traditional TPP methods encounter OOM errors on this dataset
Methods And Evaluation Criteria: The methods are well-designed for the problem, and the evaluation criteria are appropriate and comprehensive, covering diverse datasets, tasks, and comparison points. The authors have made sensible choices in metrics and baseline comparisons that allow for a fair assessment of their contributions.
Theoretical Claims: There is no theoretical contribution.
Experimental Designs Or Analyses: 1. The Chronos's performance is bad based on the results shown in Table1. It should be more analysis or more TS foundations, such as TEMPO, involved in the experiments to understand the fundamental results.
2. Can the NeuralODE-based solution such as LipCDE[1] be used to address such irregular time series task?
[1] Cao, D., Enouen, J., Wang, Y., Song, X., Meng, C., Niu, H., & Liu, Y. (2023, June). Estimating treatment effects from irregular time series observations with hidden confounders. In Proceedings of the AAAI Conference on Artificial Intelligence (Vol. 37, No. 6, pp. 6897-6905).
Supplementary Material: The supplementary material is the same as the submission.
Relation To Broader Scientific Literature: The key contributions of LAST SToP relate to the broader scientific literature by: (1) addressing limitations of traditional Temporal Point Processes that struggle with large event spaces and natural language descriptions; (2) bridging the gap between foundation models for time series (like Chronos) and asynchronous time series modeling; (3) extending Parameter-Efficient Fine-Tuning approaches like soft prompts with a novel stochastic training method that parallels techniques from other domains like dropout and Matryoshka Representations; and (4) demonstrating that LLMs can effectively model complex temporal data beyond their traditional text domain, complementing efforts like TimeLLM and LLMTime which focused on regular time series.
Essential References Not Discussed: As mentioned in the previous answers, there could be more NeuralODE-based related works.
Other Strengths And Weaknesses: 1. Creative Integration of Concepts
- The paper creatively combines soft prompting approaches with stochastic training techniques, drawing inspiration from areas like dropout and Matryoshka representations to create a novel adaptation mechanism.
- The authors' approach to viewing asynchronous time series as natural language data is an elegant shift in perspective that leverages the strengths of LLMs.
2. Practical Applicability
- The method addresses real-world challenges in handling asynchronous time series data, which appear in numerous important domains (healthcare, finance, e-commerce, social media).
- The parameter-efficient nature of SToP (using only 0.02% of model parameters) makes it practical for deployment in resource-constrained environments.
3. Technical Innovation in Training
- The stochastic prefix selection during training is a simple yet effective innovation that produces measurable benefits in representation quality and training speed.
- The observed coarse-to-fine structure in learned prompts suggests an interesting emergent property that could have broader applications in prompt tuning.
4. Comprehensive Analysis
- The paper provides thorough analyses (t-SNE visualizations, cosine similarity measurements, model probing) that give insights into why their method works.
- The scaling experiments across different model sizes (1B, 3B, 8B) demonstrate the approach's robustness and future potential.
Weaknesses
1. Limited Analysis of Domain-Specific Performance
- While the paper tests on datasets from different domains, there's limited analysis of how performance varies across domains and why certain domains might benefit more from the approach.
- A deeper exploration of domain-specific challenges and how the method addresses them would strengthen the paper.
2. Theoretical Foundations
- The paper lacks theoretical grounding for why SToP works better than standard soft prompting. While empirical results are strong, a more formal analysis would strengthen the contribution.
- The connection between the stochastic training procedure and the emergence of coarse-to-fine structure could be better explained.
Practical Implementation Details
Other Comments Or Suggestions: - The paper would be strengthened by including some concrete examples of model predictions compared to ground truth, especially for cases where the model performs particularly well or poorly.
- Visualizing how predictions differ across methods could provide intuition about the advantages of LASTS.
Questions For Authors: What can we exactly learn from the Figure 5 and Figure 13?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for recognizing the creative integration of concepts, practical applicability, innovation in training techniques, and comprehensive analysis in our work. Responses to key points raised:
**Chronos: Limited analysis; inclusion of TEMPO:** Chronos performs poorly as expected, given its reliance on time series–specific augmentations and synthetic data, which make it ill-suited for asynchronous time series due to their fundamental differences (L046–L020). We included Chronos as a representative general-purpose TS model to highlight how such assumptions hinder performance, unlike models like LLMTime and LLMProcesses that incorporate fewer biases. which likely contributes to their stronger performance.
Thanks for pointing us to TEMPO; it faces similar limitations due to its reliance on seasonal and trend decomposition—concepts not meaningful for asynchronous sequences. These comparisons underscore the need for purpose-built approaches like LASTS. We will revise the manuscript to clarify this discussion.
**NeuralODEs, LipCDE:**
Thanks for bringing up NeuralODE-based approaches like LipCDE. NeuralODEs are generally ill-suited for modeling asynchronous time series due to two key limitations:
1. In ODE systems, the future trajectory is entirely determined by the initial state, which implies that modeling long asynchronous time series would require the initial state to encode all future observations—an unrealistic assumption for most real-world data.
2. The continuous trajectories assumed by NeuralODEs make them ill-suited for capturing abrupt changes or irregular time gaps, which are common in asynchronous time series with discrete, sudden shifts.
Thus, NeuralODEs are only appropriate when underlying dynamics are deterministic and continuous, which is rarely true in practice. To our knowledge, no NeuralODE-based models have been evaluated on the datasets used in this paper.
**Weaknesses**
1. **Domain-Specific Analysis:**
We agree that domain-specific analysis can offer additional insights. In our work, we chose to focus on generalizability across 8 diverse datasets spanning 7 distinct domains given the broad ICML audience which makes it difficult to derive domain-specific conclusions. However, we make following observations to be included in teh camera-ready version:
- Online Shopping (amazon): As discussed in L371–373, the Amazon dataset includes a mix of unrelated event types grouped under one label, which possibly hurts time prediction.
- Cooking: Datasets like Breakfast and EPIC-KITCHENS show strong performance, as our model benefits from rich natural language descriptions and meaningful event sequences.
- Sports (MultiTHUMOS): This dataset features more Markovian event transitions, making forecasting relatively easier but anomaly detection harder.
2. We answer this in two parts:
- **Theoretically, why SToP is better than SP:** Our focus in this work is to demonstrate empirically, across multiple tasks and datasets, that SToP outperforms soft prompting—both in performance (Table 1) and in the structure of learned tokens (Section 4.5). We agree that a theoretical foundation would be valuable, but given the complexity, we are exploring this as future work.
- **Coarse-Fine Structure Emergence:** This emergence is a direct consequence of random prefix length selection during training which encourages early tokens to capture general patterns, while later tokens refine the representation. Similar behaviours are observed in prior work discussed in our manuscript (L254-260) :
- **Soundstream's** residual vector quantization (RVQ), where selecting a random number of quantizers during training leads to coarse-to-fine audio reconstruction, and
- **Matryoshka Representations**, which explicitly optimize for informative prefixes.
We will incorporate this discussion in the final version of the paper.
3. **Practical Implementation Details:** We're happy to clarify any remaining implementation details, revise the manuscript as needed, and will release the code upon publication.
**Other Comments: Examples and Visualization:** Thank you for the suggestion. Due to space constraints, we cannot include this analysis in the rebuttal but will incorporate it in the camera-ready version.
**Questions**
1. **What do we learn form Fig 5 & 13:** We hypothesize the emergence of a coarse-to-fine structure in SToP, where earlier tokens capture diverse high-level features, and later tokens refine them:
- **Fig5** the t-SNE projection shows that the first 100 tokens in SToP are more spread out compared to the clustered tokens in standard soft prompting. This indicates that SToP learns more diverse representations in earlier tokens.
- **Fig13:** shows that the cosine similarity between adjacent tokens is lower at the beginning of the SToP prompt and gradually increases, consistent with a coarse-to-fine pattern. No such organization is observed in standard soft prompting.
Thank you for your thoughtful review. | Summary: This paper presents LASTS, a novel framework that uses large language models (LLMs) to model asynchronous time series—sequences of events that occur at irregular intervals and are described in natural language. Unlike traditional methods that rely on fixed time intervals and predefined event categories, LASTS leverages the semantic richness of event descriptions and irregular timing to enable LLMs to perform tasks such as forecasting, anomaly detection, and data imputation. The authors also propose Stochastic Soft Prompting (StoP), a new prompt tuning technique that improves model performance by randomly truncating soft prompts during training, resulting in more diverse and generalizable representations. Through extensive experiments on real-world datasets, including action recognition and temporal point process benchmarks, LASTS consistently outperforms existing methods and demonstrates strong adaptability across different tasks. The approach offers a flexible and efficient alternative to conventional time series models and highlights the potential of LLM-based solutions for complex temporal reasoning.
Claims And Evidence: Most claims in the submission are supported by clear and convincing evidence. The authors provide comprehensive experimental results across multiple datasets and tasks (forecasting, imputation, anomaly detection) to demonstrate the effectiveness of their method. They also include strong baselines for comparison, such as traditional TPP models, foundation models, and other LLM-based approaches. The performance gains of the proposed LASTS framework and Stochastic Soft Prompting are consistently shown. However, one potential limitation is the relatively weaker time prediction performance compared to some TPP models, which the authors acknowledge but do not fully address with additional modeling strategies.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria are appropriate for the problem of modeling asynchronous time series. The use of natural language-based prompts aligns well with the irregular and semantically rich nature of such data. The selected tasks—forecasting, imputation, and anomaly detection—are relevant and practical. The chosen datasets, including both real-world temporal point process and action recognition data, provide a comprehensive benchmark. However, incorporating more diverse anomaly detection baselines or real-world industrial datasets could further strengthen the evaluation.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experimental design appears generally sound, with a reasonable choice of tasks, datasets, and evaluation metrics. The use of multiple baselines and both zero-shot and fine-tuned settings adds credibility to the results. At a glance, there are no obvious flaws, but a deeper look would be needed to verify the robustness of all experimental components.
Supplementary Material: I briefly looked through the supplementary material. Most of the appendix appears to provide supporting details such as prompt templates, dataset preprocessing, and additional quantitative results. These sections mainly serve to reinforce the main paper rather than introduce new claims or critical insights. While useful for completeness and reproducibility, the appendix does not present fundamentally new contributions beyond what is already discussed in the main text.
Relation To Broader Scientific Literature: The key contributions of the paper build on and extend several existing directions in the broader scientific literature. First, it advances the emerging line of work that explores using large language models for time series tasks by adapting them to irregular, event-based sequences rather than traditional regularly sampled data. Second, it connects to research on prompt-based learning and parameter-efficient fine-tuning, introducing a novel variant—Stochastic Soft Prompting—that aligns with broader trends in reducing adaptation cost for large models. Finally, the work challenges the conventional reliance on specialized architectures like temporal point processes by demonstrating that general-purpose language models, when properly prompted, can handle a wide range of temporal reasoning tasks, contributing to the growing movement toward more unified, flexible modeling approaches across domains.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their detailed review. We appreciate the recognition of our method's novelty, the thoroughness of our experimental evaluation, and the relevance of our chosen tasks and benchmarks. We also thank the reviewer for highlighting how our work aligns with broader scientific trends—adapting LLMs to new domains, advancing parameter-efficient fine-tuning techniques, and challenging the reliance on specialized architectures.
We acknowledge the two specific areas of improvement identified and address them below:
1. **Relatively weaker time prediction performance compared to TPP models**:
We agree with the reviewer, however, our design prioritizes simplicity, general applicability across tasks (forecasting, imputation, and anomaly detection), and effective use of diverse natural language event descriptions—without explicitly modeling time. This leads to our model ranking as best on 13 and in the top 2 on 17 out of 18 evaluations in Table 2. Introducing explicit time modeling is a valuable next step, which we are actively exploring as future work.
2. We answer this in two parts:
- **Anomaly detection baselines:** This task remains underexplored in the context of asynchronous time series. While we have adopted someTime Series methods (e.g., Chronos, LLM Processes) to the asynchronous setting for forecasting and imputation, they cannot be easily extended to anomaly detection as they are very forecasting focused and anomaly detection is not easily recast as a forecasting problem. We see our work as an early step toward bridging this gap.
- **Inclusion of industrial datasets:** We used publicly available datasets from standard benchmarks widely adopted in the literature to ensure fair comparison with both traditional TPP models and modern time series forecasting methods. We agree that incorporating additional real-world industrial datasets could further strengthen the evaluation.
We thank the reviewer again for their insightful feedback, and are happy to answer any additional questions. | null | null | null | null | null | null |
HyperNear: Unnoticeable Node Injection Attacks on Hypergraph Neural Networks | Accept (poster) | Summary: This paper focuses on the vulnerability of hypergraph neural networks (HNNs) to node injection attacks. The authors introduce HyperNear, a novel node injection attack method specifically designed for HNNs, which exploits the homophily property to improve stealthiness. Through extensive experiments, the study demonstrates the effectiveness of HyperNear in black-box scenarios, representing a significant advancement in the field of adversarial attacks on hypergraphs. The findings underscore critical implications for the security and robustness of hypergraph-based models, offering valuable insights for future research in this area.
Claims And Evidence: Yes, the claims made in the submission are supported by clear arguments and convincing results with detailed discussion.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The paper provides a theoretical analysis on the impact of attacks on hypergraph topology and homophily, identifying two key findings: (1) Hypergraphs are highly sensitive to adversarial attacks due to their intricate interdependencies; (2) Naive attacks significantly disrupt homophily, which can be leveraged to design more subtle and effective attacks.
Experimental Designs Or Analyses: The experiments are sound and substantiate the claims made in the theoretical analysis. The empirical results effectively showcase the impact of node injection attacks on the topology and homophily of hypergraphs.
Supplementary Material: Yes, the supplementary material is comprehensive, including an additional discussion on the relationship between supernode characterization and homogeneity change, a detailed experimental setup and results, and a detailed proof procedure for the theorem presented in the main text. I have thoroughly reviewed the contents.
Relation To Broader Scientific Literature: This paper fills a gap in research on adversarial attacks against HNNs. The authors effectively position their work within the broader literature by highlighting the unique challenges posed by higher-order dependencies in hypergraphs, which have been largely overlooked in prior research on adversarial attacks. The discussion of Finding 1 and Finding 2 provides a solid theoretical foundation that connects well with existing studies on graph-based adversarial attacks.
Essential References Not Discussed: The paper has covered the relevant related works necessary to understand its key contributions.
Other Strengths And Weaknesses: Strengths:
1. The paper provides a compelling motivation for investigating node injection attacks on hypergraphs, emphasizing the unique challenges introduced by higher-order dependencies. This is an interesting and important piece of work.
2. The paper is exceptionally well-organized, making it easy to follow. The motivation, methodology, theoretical analysis, and experiments are all presented in a coherent and logical manner.
3. The experimental design is comprehensive, and the open-source code facilitates further research in the field.
Weaknesses:
1. The comparison methods lack evaluation of stealthiness.
2. Where applicable, include summary rows or average performance rows to make it easier to compare the overall effectiveness of HyperNear against baselines.
Other Comments Or Suggestions: 1. Ensure that the main text references key sections of the supplementary material to guide readers through the additional content.
2. Ensure consistent font styles across all figures.
3. Increase the font size of the figures in the Experiments section.
Questions For Authors: See the weaknesses and the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We sincerely appreciate your **comprehensive and positive evaluation** of our work, particularly your recognition of our **theoretical contributions, experimental rigor, and positioning within the broader adversarial attack literature on hypergraphs**. Your feedback reinforces the significance of our study and motivates future research in this area. Next I address your concerns point by point.
Weakness 1: In our paper, we have already evaluated the homophily shift for the ''Random'' baseline to illustrate stealthiness. Additionally, Figure 8 **provides a comprehensive analysis of how other attack methods (NDA, FGA) affect homophily across different datasets (DBLP-CA, Cora, Pubmed, Citeseer)**. This effectively demonstrates the stealthiness variations among different attack strategies. Your suggestion is valuable, and we will consider adding a table with homophily change metrics for other methods in the revised manuscript.
Weakness 2: To improve the clarity of performance comparisons, we have added a summary row to the table that presents the average performance drop for each attack method relative to the ''Clean'' baseline. This allows for a more intuitive comparison of the overall impact of HyperNear against other methods.
| Victim Model | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR |
|--------------------|-------|--------|------|------|-----------|-------|--------|------|------|-----------|-------|--------|------|------|-----------|-------|--------|------|------|-----------|
| Methods | | | | | | | | | | | | | | | | | | | | |
| UniSAGE | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR | Clean | Random | NDA | FGA | HyperNEAR |
| Avg. Drop ↓ | - | 0.13 | 2.59 | 2.53 | 14.82 | - | 0.2 | 2.75 | 2.93 | 13.97 | - | -0.18 | 2.65 | 0.65 | 8.13 | - | -0.48 | 2.67 | 1.01 | 8.53 |
Suggestion 1: Thank you for the suggestion to improve cross-referencing between the main text and the supplementary material. We will scrutinize our manuscript againto **ensure that the reader is clearly directed to the relevant supplemental chapters** that provide more detail.
Suggestion 2: Yes. We will ensure consistent font styles across all figures for a more polished presentation.
Suggestion 3: We will increase the font size in the experimental figures to improve readability.
Thank you again for recognizing this work and for your constructive comments.
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Rebuttal Comment 1.1:
Comment: The authors have provided clear and satisfactory responses to the points I previously raised. I have also skimmed through their replies to the other reviewers, which reinforce my positive assessment regarding the originality and significance of the work. I have no remaining concerns and consider the paper ready for acceptance. Therefore, I am happy to update my score and recommend an SA.
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Reply to Comment 1.1.1:
Comment: Thank you for acknowledging our clarifications and responses, as well as for your positive assessment of our work.
Your constructive comments and suggestions have been instrumental in helping us further enhance the clarity and quality of our paper. We truly appreciate your time and support throughout the review process. | Summary: This work introduces HyperNear, a homophily-preserving node injection attack for hypergraph neural networks (HNNs). It provides a theoretical analysis of hypergraph vulnerability and demonstrates that homophily can be leveraged to enhance attack stealth. Extensive experiments show that HyperNear is highly effective and unnoticeable, making it the first black-box attack framework for HNNs, with important implications for hypergraph security.
Claims And Evidence: The claims are well-supported by the presented evidence. The authors demonstrate that hypergraphs are vulnerable to node injection attacks through empirical analysis and propose a novel attack framework, HyperNear. The results show strong performance and generalization, validating their claims.
Methods And Evaluation Criteria: The proposed methods are appropriate for the problem. The authors introduce a tailored attack framework for HNNs and evaluate it using extensive experiments in a black-box setting. The approach is sound and demonstrates effectiveness.
Theoretical Claims: Yes. I have checked carefully the proofs and details. Theorem 3.1 and Corollary 3.2 are well-grounded.
Experimental Designs Or Analyses: The experimental design is well-structured, and the theoretical analysis is clearly presented and sound. I have carefully reviewed the relevant details and found them to be appropriate and convincing.
Supplementary Material: Yes, I have checked the supplementary material. A detailed theoretical derivation process and more experimental details are presented there. All the contents provide more support for my evaluation of this work.
Relation To Broader Scientific Literature: The paper introduces a valuable contribution to adversarial attacks on hypergraphs. The study of vulnerabilities in graph neural networks is an active area of research. This paper extends this line of inquiry to hypergraphs, offering novel insights that are relevant to both theoretical and applied researchers.
Essential References Not Discussed: The paper provides a comprehensive overview of relevant works on HNNs and adversarial attacks on graph data. No critical gaps in the literature review were identified based on the provided context.
Other Strengths And Weaknesses: Strengths
Novelty: The introduction of HyperNear as a node injection attack specifically designed for HNNs is a strong contribution.
Clear Motivation: The introduction effectively explains the research motivation. It contrasts traditional injection strategies with the paper’s core issue—achieving effective and stealthy attacks in hypergraphs. This sets a clear direction for the research.
Clear Mathematical Formulations: The paper rigorously defines its attack methodology and impact analysis.
Strong Empirical Results: The experiments show that HyperNear is effective across multiple datasets and models.
Weaknesses
1.The diagram in Figure 4 is somewhat unclear. It would be helpful to provide more context or explanation in the caption to clarify what the classification results represent and how they support the paper’s claims about the attack's effectiveness. Additionally, improving the visual clarity (e.g., clearer legends, or annotated highlights) could make the figure more informative.
2.Figures 1(a) and 1(b) could better illustrate how injected nodes integrate into the network through homophily, beyond just connections and attributes. This would highlight the role of homophily in stealthiness more clearly.
3.The authors have conducted experiments on five datasets (Cora-CA, DBLP-CA, Citeseer, Cora, and Pubmed), which effectively demonstrate the potential of HyperNear. To further strengthen their findings, it might be beneficial to explore a more diverse range of datasets. This would help ensure that the method remains effective across different scenarios.
Other Comments Or Suggestions: 1.The font size in Table 1 could be increased to improve readability.
Questions For Authors: 1.The paper states that hypergraphs' intricate dependencies can amplify the effects of small perturbations. Could you provide a more explicit quantitative measure or theoretical derivation to demonstrate this amplification effect?
2.I'm curious why the theoretical analysis in the paper focuses primarily on homophily. Is this the only or the best measure to evaluate the impact of hypergraph attacks?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your detailed review and for recognizing the novelty and contributions of our work, including the introduction of HyperNear, its theoretical grounding, and its strong empirical results. Below, we address your comments point by point.
Weakness1: Figure 4 illustrates the difference in the distribution of homophily ratio before and after the attack. We will refine Figure 4 by enhancing its clarity, improving the legend contrast, and adding explanatory annotations to highlight how classification results support our stealthiness claims. Thank you for your valuable suggestions.
Weakness2: We clarify that Figure 1(a) is designed to illustrate **how the impact of injected malicious nodes propagates through the hypergraph topology**, rather than demonstrating homophily-guided injection. Meanwhile, we acknowledge that Figure 1(b) could better highlight homophily's role in stealthiness. To improve clarity, we will enhance the figure and captions to better convey these distinctions.
Weakness3: Thank you for the suggestion. The five datasets we use are widely adopted benchmarks in hypergraph learning, making them appropriate for evaluating HyperNear. However, we agree that exploring additional datasets could further reveal the impact of hypergraph structure on attack robustness. We consider this an important direction for future work.
Other 1: We will increase the font size in Table 1 to improve readability.
Question 1: Our paper already provides a theoretical analysis of how hypergraph topology influences homophily and how local perturbations can cascade through the structure. Specifically, Theorem 3.1 formalizes how perturbations affect node relationships, **with the first term capturing linear propagation effects, while higher-order terms reflect nonlinear amplification**, which can become significant under large perturbations or varying hyperedge weights.
Additionally, **Figure 11** illustrates how perturbations propagate in HNNs, visually demonstrating this cascading effect. The primary term dominates for small perturbations, ensuring controlled degradation, while higher-order dependencies introduce more complex, nontrivial effects under larger structural changes.
Question 2: In hypergraphs, **homophily quantifies the similarity of connected nodes in feature space**, making it a natural and intuitive measure of structural changes. Since **hypergraph neural networks heavily rely on homophily for information propagation**, perturbing homophily can significantly degrade model performance, which aligns with our attack objectives.
As discussed in our paper, **exploring alternative structural change metrics in hypergraphs is an important future research direction**. While homophily provides a strong foundation, other potential measures could offer complementary insights into structural vulnerabilities.
Once again, we sincerely appreciate your thoughtful feedback and your recognition of the novelty and significance of this work. Your comments have helped us refine our presentation and identify valuable directions for future research. | Summary: This paper proposes a black-box node injection attack on Hypergraph Neural Networks (HNNs), named HyperNear. Unlike previous gradient-based white-box attacks on HNNs, this method does not require access to model parameters or gradients. Instead, it strategically injects malicious nodes and optimizes their connections to maintain high homophily, making the attack less detectable. The paper formulates the attack as an optimization problem, balancing attack effectiveness and stealthiness. Experimental results demonstrate that HyperNear significantly degrades classification performance while maintaining structural similarity to the original hypergraph, suggesting its robustness in real-world scenarios.
Claims And Evidence: The paper claims that HyperNear effectively degrades HNN classification performance while remaining stealthy due to homophily-aware node injection. While the empirical results support the performance degradation claim, the assertion that homophily-based attacks are harder to detect lacks rigorous mathematical or experimental justification. Additionally, the paper does not discuss whether existing adversarial defense mechanisms can counteract this attack, leaving its robustness against defenses unclear.
Methods And Evaluation Criteria: The proposed method aligns with the problem setting, leveraging node injection to attack HNNs under a black-box assumption. The evaluation uses standard benchmark datasets, which are appropriate for assessing classification performance.
Theoretical Claims: The paper provides a mathematical formulation for the attack optimization process, defining the objective function that balances attack effectiveness and stealthiness, though it lacks formal guarantees on its convergence and optimality.
Experimental Designs Or Analyses: The experimental design follows standard practices, evaluating the attack on benchmark datasets with classification accuracy as the primary metric. The results demonstrate a clear performance drop, supporting the attack's effectiveness.
Supplementary Material: Yes, I have checked supplementary material.
Relation To Broader Scientific Literature: The paper extends prior work on adversarial attacks against HNNs by shifting from gradient-based white-box methods to a black-box node injection attack, aligning with broader research on adversarial robustness in graph-based learning. It builds on the concept that homophily influences attack effectiveness, which has been explored in GNN adversarial studies but is less studied in hypergraph settings.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
S1. Novel black-box attack formulation for HNNs.
S2. Optimization framework balances attack effectiveness and stealthiness.
S3. Empirical evaluation on multiple benchmark datasets.
Weakness
W1: As described in the Related Works section, previous studies have already proposed gradient-based adversarial attack methods for HNNs. Therefore, the key focus of this work should be on transferring the attack to a black-box setting. I believe the novelty and motivation should emphasize black-box attacks rather than HNNs themselves.
W2: In Figure 1(b), I do not clearly see the distinction between Homo. and Hete.. Although I eventually realized that the authors might be trying to illustrate that injection attacks targeting Homo. structures are harder to detect, this conclusion requires strict mathematical or experimental support.
W3: The paper does not seem to discuss whether existing adversarial defense methods can detect or mitigate this attack.
Other Comments Or Suggestions: None
Questions For Authors: Q1: Compared to black-box attacks on GNNs and white-box attacks on HNNs, what are the key challenges of this paper’s attack on HNNs?
Q2: Can the attacker obtain complete information about the hypergraph? If they have full access to the graph structure and node attributes, would this still be considered a black-box attack?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Claims&W2&W3: Thank you for your valuable feedback and for recognizing the effectiveness of our attack methodology.
Our claim of stealthiness is based on the observation that homophily-aware attacks introduce perturbations aligned with existing structural patterns, making them less detectable than naive attacks. While **Figure 4 & 5 provide empirical evidence**, we acknowledge the need for stronger theoretical justification. Regarding adversarial defenses, existing graph-based methods may not directly apply to hypergraphs due to structural differences. Evaluating robustness against hypergraph-specific defenses is an important direction for future work.
To the best of our knowledge, no prior work has established attack methods for hypergraphs. Our study serves as an exploratory step, proposing the first black-box attack framework for hypergraph neural networks, which is a fundamental prerequisite for systematic defense research. Given the absence of standardized adversarial defenses in hypergraph learning, we deliberately **prioritize vulnerability analysis over premature defense development**, aligning with security research paradigms in graph learning [4], where attack understanding precedes defense formulation. We believe **this work lays a crucial foundation for future robustness studies in hypergraph learning**.
Theoretical: Thank you for recognizing our mathematical formulation of the attack optimization process, which balances effectiveness and stealthiness. While we do not provide formal convergence guarantees, this is due to the complexity of hypergraph structures, where high-order dependencies and discrete perturbations make theoretical analysis non-trivial. Nevertheless, **our empirical results consistently demonstrate stable and effective attack performance across multiple datasets**. Future work could explore theoretical analyses, such as proving convergence under specific constraints or employing continuous relaxations of the attack space.
W1: While we agree that black-box attacks are a key contribution, our work is not merely about transferring existing attacks to a black-box setting. Instead, we position this as an exploratory study into the fundamental vulnerabilities of hypergraph neural networks under adversarial attacks, an area that has received little attention.
Notably, every reviewer recognized our work as a promising and significant direction, **highlighting the importance of understanding adversarial threats in hypergraphs**. Our study emphasizes the challenges posed by the higher-order dependence of hypergraphs and the need for homophily-aware perturbations. We further elaborate on these challenges in Q1, where we discuss the difficulty of designing attacks that remain stealthy while coordinating complex hypergraph structures.
W2: Thank you for the suggestion. We will enhance Figure 1(b) by improving color contrast, making the distinction between homophilous and heterophilous hyperedges more visually intuitive. For concerns regarding formal proofs, please refer to our response to Claims&W2&W3.
Q1: Compared to black-box attacks on GNNs, perturbations in **standard graphs only affect pairwise connections, while in hypergraphs, a single hyperedge impacts multiple nodes**. This requires coordinated modifications to remain stealthy, making attack design significantly harder.
Compared to white-box attacks on HNNs, **our black-box setting lacks access to model parameters or gradients**, requiring surrogate models and heuristic strategies.
Moreover, hypergraph attacks require greater stealth, as their intricate interdependencies render naive perturbations more easily detectable. Additionally, while hypergraphs have attracted growing interest for their strong representational capabilities, the study of homophily in hypergraphs has only recently begun to receive attention [5]. The structural complexity of hypergraphs makes the homophily problem particularly challenging and still largely underexplored.
Q2: We follow the strict black-box setting in [6], where attacker can access node features but has no knowledge of model parameters or gradients. Therefore, using original feature for feature generation is consistent with this definition. In addition, the use of raw features belongs to the reasonable a priori knowledge of the attacker (e.g., publicly available user features are observable by the attacker in social networks) and **does not conflict with the black-box setting**.
Thank you again for recognizing this work and for your constructive comments.
[4] Zügner et al., Adversarial Attacks on Neural Networks for Graph Data. In KDD, 2018.
[5] Li et al., When Hypergraph Meets Heterophily: New Benchmark Datasets and Baseline. In AAAI, 2025.
[6] Xu et al., Blindfolded Attackers Still Threatening: Strict Black-Box Adversarial Attacks on Graphs. In AAAI, 2022. | Summary: The authors proposed a node injection attack algorithm for hypergraph neural networks in black-box setting.
Claims And Evidence: Problematic claims:
1. Un-noticability: I do not understand why the authors claim unnoticability where Figure 4(a) clearly distinguishes that "After attack" distribution is bimodal while "before attack" distr. is unimodal. Similarly, Figure 5(b) shows that one can identify the injected nodes in the periphery region.
2. Black-box claim. In the Feature Generation step of the algorithm, since the attacker uses the original node feature x_{ori} to construct the node feature of the injected node x_{inj}, could such an attack still be considered a black box?
3. Transferability: I am confused about the setting of the transferability experiment as it is not discussed properly. Have you considered any surrogate models other than HyperGCN, HGNN, ED-HNN and UniGCNII to generate perturbed Hypergraph $H'$?
Methods And Evaluation Criteria: 1. I understand the reason to analyse Homophily distribution to justify un-noticability, but a more straightforward and practical way is to look at simpler statistics such as degree and dimension distribution.
2. However, the baseline models are inadequately discussed in section 5.1. The authors should consider explaining Random, NDA and FGA more precisely in detail. For instance, it is not clear how "randomly generating node features" work. Or what kind of modification of features are considered for the smallest deg node in NDA?
Theoretical Claims: One of the key theoretical claims of the paper shows that the topology of a hypergraph is vulnerable to adversarial attack (sec 3.1). Apart from under-explained notations (articulated in ``Other comments’’), the most problematic part is that it is not clear how hypergraphs amplify minor perturbations in comparison to graphs. A more convincing argument is lacking here.
I did not find anything specific to hypergraph structure being shown as contributing to the Amplification effect. Similar arguments can be made for graphs with GNNs aggregation. For instance, lines 184-186 say, “A single perturbation can propagate through the structure, affecting multiple nodes simultaneously and highlighting the fragility of hypergraphs.”; the same thing can be said for a graph node that is connected to multiple other nodes.
Experimental Designs Or Analyses: The x-axis in Figure 4 => Does it indicate FHH, or node-label based homophily rate? I understand the reason to analyse Homophily distribution to justify un-noticeability, but a more reasonable way is to look at simpler statistics such as degree and dimension distribution.
Supplementary Material: I checked the anonymous codebase for source codes. The supplementary material is incomplete and impossible to run.
Relation To Broader Scientific Literature: The broader direction of the paper is promising.
Essential References Not Discussed: None, to the best of my knowledge.
Other Strengths And Weaknesses: The work is promising but needs more time to be publication-ready.
Other Comments Or Suggestions: Figure 2 is not good enough. Legends are obfuscating the numbers.
Questions For Authors: 1. Lines 25-27: “These attacks are
stealthy and practical, as they avoid altering existing nodes
or hyperedges. “ - why such attacks are practical in a hypergraph context?
2. Line 17 in Algorithm 1 says, “while adversarial objective not met do .. “. What are the conditions for the objectives to meet?
3. Table 2, Why some random injection attacks are invalid?
4. Theorem 3.1, What is the nature of the perturbation $\Delta \mathcal{R}_v$?
5. Equation 7, What do you mean by ``t-hop features’’? $f_1, f_2,...,f_n$ was never properly defined before? What are the choices and properties of $f()$ and $\phi$? Do you consider them differentiable? Please properly articulate the conditions under which the theorem holds.
6. Defn 3.4, What is the definition of average degree of hyperedge $e$? Please be clear and concise.
7. Proposition 3.3, “Naive adversarial attacks cause a significant
reduction in the homophily ratio of hypergraphs,..” - What constitutes a naive adversarial attack?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We sincerely appreciate your detailed feedback and address your concerns below.
Claims1: Our claim of unnoticeability is **relative**, meaning that our attack is designed to be less detectable compared to naive perturbations. **The degree of unnoticeability also varies across datasets due to differences in hypergraph structures [1]**. For instance, Cora has a noisier and less structured hypergraph compared to Cora-CA, as their hyperedge constructions differ. Thus it produces less impact in Fig.4(b) (Cora-CA) than in Fig.4(a) (Cora).
Claims2: Yes. Please refer to our response to Reviewer FH69’s Q2.
Claims3: In addition to four surrogate models in transferability (HyperGCN, HGNN, ED-HNN, UniGCNII), Table 2 includes UniSAGE, UniGIN, UniGCN, and UniGAT, **covering diverse hypergraph neural networks** for comprehensive evaluation.
Methods1&Exp: Our study focuses on homophily because both structural and feature perturbations directly affect it, making it a better indicator of unnoticeability than degree or feature distributions, which are outside our scope. As noted in line 201, we measure homophily FHH, defining the x-axis in Figure 4. Revealing homophily’s sensitivity is a key contribution, as it captures both structural and feature-based perturbation effects.
Methods2: Random: Node features are randomly sampled from a Gaussian distribution fitted to existing node features. NDA: We select nodes with the smallest degrees and perturb their features by adding Gaussian noise proportional to feature variance. Full details are available in our public code.
Theoretical1&Theoretical2: Section 3.1 analyzes hypergraph topology's vulnerability, not its comparison to standard graphs. Hyperedges amplify perturbations differently from graphs, where message passing is pairwise. While both graphs and hypergraphs allow perturbation propagation through the structure, **their structural mechanisms differ fundamentally**. Corollary 3.2 shows hyperedge weight and feature changes impact all incident nodes simultaneously.
Supplementary: Thank you for noting this issue. The incomplete code was due to an outdated version of the repository used at the time of submission. We have **now updated it with the correct, runnable code**.
Other: We will redraw Figure 2 to improve clarity, ensuring legends do not obscure numbers.
Q1: The practicality of such attacks lies in the non-i.i.d. nature of hypergraph data, where structural dependencies significantly impact representation learning. Unlike graphs, hypergraphs propagate information across multiple entities, influencing representation learning (e.g., HGNN+ [2]).
Q2: Lines 916-927 (Appendix B) define our adversarial objective. Algorithm 1 (Line 17) terminates when further perturbations **no longer improve attack effectiveness** or when **accuracy drops below a threshold**, preventing over-perturbation and also to conserve resources.
Q3: We believe that, in some cases, random injections may unintentionally act as data enhancement, leading to performance improvements rather than degradation. This aligns with findings in contrastive learning for hypergraphs (e.g., HyperGCL [3]), where certain hyperedge augmentation can enhance model generalizability and robustness. This further justifies the need for dedicated adversarial attack studies on hypergraphs.
Q4: Theorem 3.1's perturbation $ΔR_v$ refers to **structural modifications via node injection**, altering neighborhood relationships and feature propagation.
Q5: ''t-hop features" are neighborhood features aggregated through t-hop hyperedges. Line 110 defines $f(\cdot)$ as the aggregation function, with $f_t$ representing t-hop features. We will clarify that $n$ is the maximum hop count. As noted in Line 161, both $f(\cdot)$ and $\phi$ are differentiable hypergraph convolution aggregation functions. Theorem 3.1 holds if aggregation follows Eq. (6).
Q6: Line 198 already provides the definition: the average degree of hyperedge $e$ is given by $d_e=\frac{1}{|e|}\sum_{i \in e}d_i$, ensuring balanced normalization in homophily calculations.
Q7: Naive adversarial attacks lack strategic design and inject random or heuristic perturbations without considering hypergraph structure. Our optimized hypergraph-specific attacks balance effectiveness and stealth.
We sincerely appreciate your thorough review and constructive feedback, which have greatly contributed to improving the clarity of our work. If you have any further questions or concerns, we would be glad to provide additional clarification or discussion. Thank you once again for your time and valuable input.
[1] Wang et al., From Graphs to Hypergraphs: Hypergraph Projection and its Remediation. In ICLR, 2024.
[2] Gao et al., HGNN+: General Hypergraph Neural Networks. In TPAMI, 2023.
[3] Wei et al., Augmentations in Hypergraph Contrastive Learning: Fabricated and Generative. In NeurIPS, 2022.
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Rebuttal Comment 1.1:
Comment: Thank you for your effort in the response. I keep my score due to concerns below:
Concerns about -
> Claim1:
The paper claims to be the “first work to perform a global adversarial attack on HNNs in a black-box setting”. The baselines are adaptation of attacks that were designed for graphs; not designed for hypergraphs. With such state of affairs, does it make sense to argue that the paper claims un-noticability in relative terms? See for instance, Mettack and Nettack for how to explicitly incorporate unnoticability criteria into attack algorithms.
> Claim3:
Lines 365- 368 do not mention that you tested transferability on these models: UniSAGE, UniGIN, UniGCN, and UniGAT. This is confusing. When you discuss baseline method FGA on line 302, you mention about a “hypergraph proxy model” - What kind of proxy model is this? Please clarify this.
> Methods1&Exp:
“Our study focuses on homophily because both structural and feature perturbations directly affect it, making it a better indicator of unnoticeability than degree or feature distributions” => Do you have any theoretical or empirical justification for this statement that homophily is a better indicator of unnoticability than degree or feature distributions?
> Method2:
Thanks for clarifying.
> Theoretical1&Theoretical2:
“Section 3.1 analyzes hypergraph topology's vulnerability, not its comparison to standard graphs. “ => Why one needs to perturb hypergraph directly? Why can’t we transform it into a bipartite graph (or clique graph) and do our perturbations in bipartite graph space (or graph space)? This is why the vulnerability comparison in relation to such constructions are important.
“Hyperedges amplify perturbations differently from graphs, where message passing is pairwise.” => Section 3.1 does not show how hyperedges amplify perturbations differently from equivalent graph-based constructs such as clique graph or bipartite graph.
“While both graphs and hypergraphs allow perturbation propagation through the structure, their structural mechanisms differ fundamentally.” => Not entirely true. You can transform a hypergraph to a bipartite graph, and doing so the perturbation propagation would not be any different.
**Novelty concerns**
The impact of homophily in Graph attack was already investigated in [3] for GNNs. The definition of homophily for hyperedges (Eqn 3) you defined appears to be a straightforward adaption: homophily ratio[3] of the clique representation of a hyperedge.
**Additional Suggestions:**
1. Please investigate how the performance compares with the baselines in evasion setting.
2. Please conduct efficiency studies reporting the execution time of algorithm 1, along with a runtime complexity of Algorithm 1. It is recommended to have an efficiency subsection for the attack as done in Mettack [1]
3. Please consider large-scale hypergraph datasets proposed recently such as [2] to evaluate if the attacks scales to large hypergraphs.
Refs:
[1] Adversarial Attacks on Graph Neural Networks via Meta Learning, ICLR’19
[2] Datasets, tasks, and training methods for large-scale hypergraph learning, 2023.
[3] How does Heterophily Impact the Robustness of Graph Neural Networks? Theoretical Connections and Practical Implications. KDD’22.
---
Reply to Comment 1.1.1:
Comment: >Claim1
Our contribution lies not only in proposing a black-box attack setting, but also in **designing a principled, homophily-aware strategy specifically tailored to hypergraphs**. While Metattack is a gradient-based poisoning attack on graphs via meta-optimization, directly adapting it to hypergraphs fails to preserve high-order semantics unique to hyperedges. Our baseline methods are thus adapted for the hypergraph domain under the same setting. Our claim of unnoticeability is explicitly relative, i.e., our method achieves higher stealth compared to these adapted graph baselines on the same HNN tasks.
>Claim3
As we clarified in our previous response, the results of UniSAGE, UniGIN, UniGCN, and UniGAT are already presented in **Table 2**, demonstrating that our proposed method generalizes across a broad spectrum of hypergraph neural networks.
The models added in **Lines 365–368** (HyperGCN, HGNN, ED-HNN, UniGCNII) were included to further enhance transferability coverage, not as exclusive targets.
We also clarify that in black-box poisoning scenarios, a “surrogate model” refers to any model used by the attacker to approximate the victim’s behavior. This standard terminology may have led to confusion but is widely used in adversarial literature.
>Methods1&Exp
We chose homophily as a stealthiness indicator due to its theoretical and our empirical relevance. It reflects feature consistency within hyperedges and is influenced by both structural and feature perturbations. Alternative metrics such as degree shifts showed no consistent correlation with attack effectiveness, whereas **changes in homophily aligned well with model degradation across datasets**.
We agree that combining multiple stealthiness metrics could further enhance attack characterization, and plan to investigate other topology-aware indicators as complementary tools in future work.
>Concerns on Theoretical Results
We appreciate the reviewer’s continued engagement. However, we would like to clarify a common misconception regarding the equivalence between hypergraphs and their graph-based projections (e.g., bipartite or clique graphs).
While such transformations are mathematically feasible, **they fail to preserve the original structural semantics of hypergraphs, especially when it comes to high-order interactions [1] [7] [8]**.
In Section 3.1, we therefore analyze vulnerability directly in the native hypergraph topology, not due to oversight, but precisely because **any analysis done in projected graph space would be fundamentally insufficient or misleading**. Our corollaries show how hyperedge perturbations jointly affect all incident nodes, a behavior unique to hypergraphs.
In short, the question “Why perturb hypergraphs directly?” has been extensively studied and answered by the field. We regret if this foundational distinction was not clearly communicated, though we respectfully point out that our first-round response already cited this exact work (Ref [1]: Wang et al., ICLR 2024) to support our theoretical design and claims.
>Novelty concerns
We respectfully disagree with the claim that our homophily formulation and investigation lack novelty.
First, the impact of homophily in graph attacks, as studied in [3], is explicitly acknowledged and cited in our main paper (see Line 215). Our work does not overlook prior contributions; instead, **it builds upon them and extends the homophily analysis to hypergraphs, which is a non-trivial and timely advancement**.
Our homophily formulation (Eq. 3) is not an adaptation from clique expansions, which oversimplify hyperedges. Instead, it captures native hypergraph label cohesion without transformation, aligning with recent findings [7] that highlight the need for hypergraph-specific metrics. This further confirms that **the problem we study is not a marginal tweak on known graph results but rather part of a growing and distinct research frontier**.
We also note that this perspective on novelty and homophily analysis has been positively acknowledged by other reviewers, further reinforcing the relevance and timeliness of our contribution.
>Additional Suggestions
Thank you for your suggestions. We agree that exploring efficiency and scalability is important. Due to space limits, our current submission focuses on methodological contributions and validating the proposed black-box threat model. We are extending our framework to larger-scale datasets and plan to report efficiency analyses in future work.
Nonetheless, these points do not affect the core validity of our current findings.
>Additional References
[7]Li et al., From Heterophilous Graph Learning to Heterophilous Hypergraph Learning: Exploring New Frontiers. In Technical Report at IMS-NTU joint workshop on Applied Geometry for Data Sciences Part I, 2024.
[8] Millán et al., Topology shapes dynamics of higher-order networks. Nat. Phys. 21, 353–361 (2025). | null | null | null | null | null | null |
Discrepancy Minimization in Input-Sparsity Time | Accept (spotlight poster) | Summary: The paper gives a new algorithm for discrepancy minimization over real valued matrices that nearly runs in input-sparsity time. Specifically, building on Bansal's and Larsen's previous algorithms, the authors give a
1) A combinatorial algorithm that runs in time $\tilde{O}(nnz(A) + n^3)$ time.
2) If Fast Matrix Multiplication (FMM) is allowed, then $\tilde{O}(nnz(A) +n^{2.53})$, breaking the cubic barrier for the first time.
The algorithm guarantees a coloring $x\in \set{-1,1}^n$ achieving discrepancy $O(\text{herdisc}(A) \log n \log^{1.5}m)$
They do this by introducing a host of interesting techniques, notably:
1) A new sketching method using implicit leverage‐score sampling (which is being utilised very heavily in a lot of recent papers) to quickly compute a hereditary projection (Theorem 1.3), while simultaneously avoiding explicitly calculating the entire projection matrix (the theorem is technical, this is just an informal description).
2) A “guess-and-correct” data structure that batches gaussian projections.
The paper is relatively readable, but quite frankly too technical sometimes. Intuition for the proofs of Theorems or even their utilities in the "big picture" is rarely communicated, and for a 51 pages paper, I expected significantly more handholding and intuition sharing throughout the reading journey. I've had to skip some proofs completely because they offered almost no intuition and were time sinks to verify, not to mention that they felt extremely mechanical.
Ultimately, I think the main result is interesting enough to be published in ICML since it tackles a long standing open problem, and it is clearly important, though I would've wished if the presentation was more accessible for a result of this importance.
Claims And Evidence: The paper’s claims are backed by Lemmas/Theorems which are proved in details in the Appendix.
Methods And Evaluation Criteria: Since the contribution is theoretical, and there are no experiments, the evaluation centers on computational complexity and approximation guarantees rather than empirical performance. I think this part is adequately addressed.
Theoretical Claims: I reviewed the outlines of the key proofs (notably for Theorems 1.1 and 1.3) and I think they are Kosher. However, I skipped several proofs (for example some of the parts in the long correctness proof of Algorithm 2).
Experimental Designs Or Analyses: N/A
Supplementary Material: There was no Supplementary Material provided, all the proofs are self contained in the pdf.
Relation To Broader Scientific Literature: The paper is well-situated in the existing literature on discrepancy minimisation. For example, it builds on the Bansal’s seminal SDP approach, The iterative partial-coloring method of Lovett & Meka, and Larsen's algorithm. The paper makes a significant contribution relative to these prior works.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1) As mentioned, the theoretical improvement in runtime is substantial compared to previous methods, and is interesting.
2) The paper introduces a host of technical results that might be of independent interest.
Weaknesses:
1) The technical exposition is very dense and may be a turn-off for readers not already very familiar with the literature on discrepancy theory
2) As mentioned above, some parts of the analysis and proofs (especially regarding the correctness of the algorithm) are very subtle and could benefit from additional intuitive explanations.
3) Experiments! This could've been a very easy win, and I don't see why the authors don't include even a tiny experiment for their algorithms. I understand that there is a ton of parameters to choose (various $\varepsilon, \delta$ to choose), but looking at the algorithm, I really think they could've implemented a variant on a toy dataset.
4) The constants in the proofs are not optimised, and sometimes they're laughably huge (I get it, no one likes to optimize constants in proofs, but some constants in the papers are just absurd). I suspect if more effort was put into this, it would've easily translated into a feasible practical algorithm, but alas.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the insightful comments and thorough evaluation of our paper.
### W1 and W2: Technical Density and Intuition
We appreciate the reviewer's concern regarding the technical density of our presentation. Given the complex nature of discrepancy minimization and the depth of the theoretical contributions, our initial goal was to ensure rigorous correctness. However, we acknowledge that improving readability and intuition is crucial. In the final version, we will include additional intuitive explanations and clear roadmaps to guide readers through the intricate parts of our proofs, particularly emphasizing high-level insights before delving into technical details.
### W3: Experiments
Thank you for pointing this out. We conduct the experiments to demonstrate the effectiveness of our algorithm. We focused our experimental evaluation on demonstrating the improvements achieved through the fast hereditary projection. This is because the lazy update scheme is primarily designed to leverage fast matrix multiplication. Although fast matrix multiplication theoretically has lower asymptotic complexity, algorithms based on FMM often suffer from significantly large constant factors, adversely affecting their practical runtime performance. Additionally, for practical considerations, the parameters used in the experiments do not strictly follow the theoretical suggestions in the paper.
Our experimental setup follows the matrix configurations used in Larsen’s paper.
**Uniform matrices:** Each entry of $A$ is uniformly chosen from $\\{-1,1\\}$
| Matrix Size | Sparsity | Larsen's Obj. Val. | Our Obj. Val. | Larsen's Runtime (s) | Our Runtime (s)|
|------------------|----------|--------------------|---------------|------------------|-------------|
| 400×400 | 1.0 | 54 | 56 | 2.98 | 2.16 |
| 400×400 | 0.5 | 38 | 42 | 2.90 | 1.95 |
| 400×400 | 0.1 | 14 | 20 | 2.91 | 1.90 |
| 2000×2000 | 1.0 | 140 | 148 | 345 | 164 |
| 2000×2000 | 0.5 | 96 | 99 | 334 | 156 |
| 2000×2000 | 0.1 | 46 | 47 | 331 | 152 |
| 10000×1000 | 1.0 | 132 | 140 | 378 | 63 |
| 10000×1000 | 0.5 | 92 | 97 | 374 | 62 |
| 10000×1000 | 0.1 | 42 | 44 | 375 | 62 |
**2D Corner matrices:** $A$ is constructed by choosing two sets of points in the unit square—one for rows and one for columns—and marking an entry as 1 if the row point strictly exceeds the column point in both coordinates, otherwise marking it as 0.
| Matrix Size | Sparsity | Larsen's Obj. Val. | Our Obj. Val. | Larsen's Runtime (s)| Our Runtime (s) |
|------------------|----------|--------------------|---------------|------------------|-------------|
| 400×400 | 1.0 | 30 | 32 | 2.80 | 2.15 |
| 400×400 | 0.5 | 36 | 36 | 2.79 | 2.18 |
| 400×400 | 0.1 | 17 | 18 | 2.75 | 1.93 |
| 2000×2000 | 1.0 | 52 | 58 | 347 | 170 |
| 2000×2000 | 0.5 | 83 | 92 | 350 | 169 |
| 2000×2000 | 0.1 | 45 | 46 | 350 | 171 |
| 10000×1000 | 1.0 | 46 | 52 | 386 | 65 |
| 10000×1000 | 0.5 | 76 | 77 | 374 | 60 |
| 10000×1000 | 0.1 | 37 | 40 | 375 | 62 |
Our algorithm achieves substantial speedups with only minor sacrifices in approximation guarantees. The speedup will be more significant once $m$ is much largerer than $n$, as sketching is known to work well in the regime where $m \gg n$ .
### W4: Constants
We agree with the reviewer that the constants in our current analysis primarily serve to highlight theoretical improvements. Optimizing these constants would indeed further enhance the practical applicability of our algorithm, although it would require additional effort. Nevertheless, our preliminary experiments indicate that the algorithm achieves significant improvements in runtime even without strictly adhering to the exact parameters suggested by the theoretical analysis.
We appreciate the positive assessment of our work. Thank you again for your thoughtful review.
---
Rebuttal Comment 1.1:
Comment: Appreciate it, my concerns have been addressed, and I trust you’ll follow through on your commitment to:
> include additional intuitive explanations and clear roadmaps to guide readers through the intricate parts of our proofs, particularly emphasizing high-level insights before delving into technical details
---
Reply to Comment 1.1.1:
Comment: We're glad to have addressed your concerns. Thank you for your valuable suggestions! | Summary: The authors develop a new, faster algorithm for approximate discrepancy minimization with bounds on the computation time depending on the input-sparsity. Their algorithm is optimal for "tall" matrices, i.e. m x n matrices with m being a polynomial in n.
Additionally, the accuracy of the approximation matches a previous algorithm by Larsen.
They identify five "barriers", i.e. shortcomings, in Larsen's algorithm and they claim to improve on all of them. Some of the main ideas here are:
1) using sketching matrices and "ImplicitLeverageScore" to approximate some matrices efficiently.
2) Introducing a data structure that allows batching a series of computations.
Finally, they have a variant of their algorithm which uses "Fast Matrix Multiplication (FMM)"
Claims And Evidence: The claims are supported by informal overviews of the various parts of the algorithm as well as proofs in the appendix. While I did not read the proofs in detail, the informal overview seemed convincing enough.
Methods And Evaluation Criteria: Their algorithm is compared with several existing algorithms and results in the discrepancy minimization litterature, which makes sense.
No experimental comparisons, does it actually compare in practise to existing algorithms? In particular, the previous algorithm of Larsen is accompanied by practical experiments, so it might have made sense to compare the new algorithm in practice. Of course, a purely theoretical improvement may be interesting in its own right.
Theoretical Claims: I did not read any proofs in full as they all appear in the appendix. However, I skimmed part of the proof of Theorem C.3 (page 19) in which it is claimed that a particular set of eigenvectors are orthogonal. This is not true in general, and it was unclear to me why it should be true in their proof. It might still be true, but at least I think it requires an argument.
Experimental Designs Or Analyses: Not relevant for this paper
Supplementary Material: I skimmed appendices B and C, mostly for typos or sentences that are unclear and not much proof verification.
Relation To Broader Scientific Literature: The paper provides a fairly thorough overview of existing theoretical results and previous algorithms in discrepancy minimization. Additionally, several applications of discrepancy minimzation are mentioned, although these are kept pretty vague.
The most important references are the algorithms by Larsen (2023) and Eldahn & Singh (2018).
Essential References Not Discussed: The discussion of the literature seems appropriate.
Other Strengths And Weaknesses: The results themselves seem fine. It might not be the most original work, since it seems to mostly consist of several existing algorithms stitched together. However, in terms of technical depth, it is well beyond most NeurIPS papers.
I'm unsure whether the paper fits the scope of the conference. There may be applications to machine learning, but the paper itself seems to have very little to do with machine learning and would probably fit better at a TCS venue. The authors also do not give convincing arguments that the paper belongs in a machine learning conference.
Finally, there are simply too many typos and weird, unclear phrases that don't make sense, especially in the appendices. This is very distracting and makes for a tedious reading experience. See "Other Comments or Suggestions" for some examples.
Other Comments Or Suggestions: List of typos and unclear phrases:
Typo p. 22: "proof of suceed probability" should be "proof of success probability"
Typo p. 15: "For convinient" should be "For convenience"
Typos p. 16, "It is well-known that random Gaussian matrices an AMS matrices gives JL-transform property" should instead be
"It is well-known that random Gaussian matrices and AMS matrices give JL-transform property".
Typo p. 20, "we now proof" should be "we now prove"
On p. 24, it says "expectated time". Expectated is not a word, should probably be "expected time".
On p. 24, there should probably be a "such that" or something similar before the inequality in the statement of Lem. E.1, right after "eta \in R".
Typo p. 26: It says "have have" at the bottom of the page.
On page 26, it says "the number entries reach the absolute value 1 keeps increasing" which makes very little sense to the point where I'm not sure what the sentence is trying to convey.
Typo page 27: The last "We" should not be capitalized in Corollary E.3.
Typo pages 27 and 28: "fourth" should be "fourth".
Typo in definition E.4. Should be "which is implicitly maintained..." instead of "which implicitly maintained..."
On page 30, should it not be g_t in "we first assume that, we add mu \cdot g"?
On page 30, on the bottom of the page it says "there must be at least one entry i \in [n] satisfying that ..." the two equations that come after this are identical which surely must be a mistake? Additionally, there is a | too much at the beginning of the second equation here here.
On page 31 at the top, what does it mean that a set is larger than a number?
In Lem. E.2, and Cor. E.3 it says (0,1)^n - should this not be (-1,1)^n?
In definition E.5, what does it mean that a vector g_t is sampled from a univariate Gaussian N(0,1)? Are the coordinates i.i.d from this distribution?
Questions For Authors: - Do you think your algorithm would be competitive in practice with the previous algorithm by Larsen?
- Can you give some further examples of why discrepancy minimization is interesting for the ML community?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the valuable feedback.
### Theoretical Claims: The proof of Theorem C.3 (page 19) claimed that a particular set of eigenvectors are orthogonal, which is not true in general.
Because any real symmetric matrix admits an orthogonal diagonalization, its eigenvectors can always be taken to be orthonormal.
### W1: Originality and connection to existing methods
While our work builds upon Larsen's algorithm and Lovett–Meka random walk method, we would like to highlight the significant theoretical and algorithmic advances introduced in our work:
- We introduce an innovative implicit leverage-score sampling technique, enabling us to significantly reduce the computational complexity of hereditary projection from Larsen’s original $O(mn^2)$ (or $O(mn^\omega)$ with fast matrix multiplication) to $O(nnz(A)+n^{\omega})$. This improvement is crucial, particularly for sparse input matrices.
- We provide a robust theoretical analysis that carefully manages error accumulation introduced by randomized sketching methods. Such robustness was not previously established and represents a substantial methodological advancement over existing discrepancy minimization frameworks.
- The lazy-update mechanism we introduce to efficiently implement the iterative Edge-Walk algorithm fundamentally reduces computational complexity from Larsen’s $O(mn^2+n^3)$ to our result of $\tilde{O}(nnz(A) + n^{2.53})$. This addresses and overcomes a significant computational barrier identified in prior literature.
### W2 and Q2: Interest to the ICML community and applications in ML
Thanks for pointing this out. We argue that the broad relevance of discrepancy theory to the ICML community stems from its strong connections to central themes in machine learning. Specifically, discrepancy minimization intersects significantly with computational learning theory [1,2], computer vision [3], unsupervised learning [4], attention KV caching [5], differential privacy [6], and sampling [7,8].
More specifically,
[1,2] introduces the relationship of discrepancy and concepts in learning theory such as VC dimension, PAC learning.
[3] introduces a method to learn hash functions via discrepancy minimization. Learning hash functions in content-based image retrieval optimize binary codes to preserve similarity in high-dimensional feature spaces, enabling faster and more efficient image search.
[4] leverage discrepancy minimization for unsupervised graph matching by aligning predictions from classical solvers and neural models.
[5] proposed an algorithm for compressing the KV cache recursively using a geometric correlated sampling process based on discrepancy theory
[6] investigated the relationship between discrepancy minimization and differential privacy in the context of linear queries over histograms.
Quasi-Monte Carlo methods [7,8] leverage concepts from discrepancy theory by employing low-discrepancy sequences to efficiently approximate high-dimensional integrals and expectations.
In the final manuscript, we will explicitly clarify and elaborate on these connections to further emphasize the relevance and significance of our work to the ICML audience.
[1] Matousek, Jiri. Geometric discrepancy: An illustrated guide. 2009
[3] Karnin, Zohar, and Edo Liberty. Discrepancy, coresets, and sketches in machine learning. COLT’19
[3] Chen, Zhixiang, et al. Deep hashing via discrepancy minimization. CVPR’18
[4] Wang, Runzhong, Junchi Yan, and Xiaokang Yang. Unsupervised learning of graph matching with mixture of modes via discrepancy minimization. TPAMI’23
[5] Han, Insu, et al. BalanceKV: KV Cache Compression through Discrepancy Theory. arXiv preprint:2502.07861
[6] Nikolov, Aleksandar, Kunal Talwar, and Li Zhang. The geometry of differential privacy: the sparse and approximate cases. STOC’13
[7] Lyu, Yueming, Yuan Yuan, and Ivor Tsang. Subgroup-based rank-1 lattice quasi-monte carlo. NeurIPS’20
[8] Lyu, Yueming. Fast rank-1 lattice targeted sampling for black-box optimization. NeurIPS’23
### W3: Typos
We sincerely appreciate the detailed list of typos and suggestions provided by the reviewer. We will carefully proofread the manuscript, correcting all listed typographical errors and ensuring clarity in terminology and statements. We recognize that readability and precision are crucial, particularly in technical papers, and will make substantial efforts to improve the overall presentation quality.
### Q1: Competitiveness relative to Larsen’s algorithm
Thank you for pointing this out. We conduct the experiments to demonstrate the effectiveness of our algorithm. Due to space limit, please refer to the rebuttal to the reviewer ZGyW for the experiment results.
We sincerely appreciate your valuable feedback, which will significantly help us improve our paper. We hope that we have adequately addressed your concerns. Please do not hesitate to reach out if you have any further questions or comments. Thank you once again for your thoughtful review. | Summary: The paper is on discrepancy minimization for real matrices - goal is to develop constructive methods that exploit input sparsity. Algorithmic discrepancy is a well-studied topic in TCS and there have been many breakthroughs in the last 15 years, starting with Bansal. Recently there was a result for binary matrices based on sparsity. This paper obtains an analogous result for real-valued matrices.
The main technique is basically dig into Larsen's algorithm, identify all the barriers to improve Larsen's algorithm for sparse real matrices. Then, the idea is to bring in techniques from randomized linear algebra and sketching to save computation. It is not straightforward since there are several steps involved and naive ways could lead to error accumulation. Besides carefully using these tools, tightening/modifying the analysis of Larsen, the paper also introduces new techniques including an implicit leverage score sampler and efficiently implementing certain random-walk based rounding step.
Claims And Evidence: Yes - don't see any problems.
Methods And Evaluation Criteria: Theory work.
Theoretical Claims: Yes - don't see major problems.
Experimental Designs Or Analyses: Theory work.
Supplementary Material: Some proofs. The paper is too long and it is hard to verify all the details/calculations.
Relation To Broader Scientific Literature: Improvement to the running time of real-valued matrix discrepancy.
Essential References Not Discussed: Looks adequate.
Other Strengths And Weaknesses: +ves
+ Makes good progress on an important combinatorics / algorithmic question
+ The techniques are non-trivial and this area is usually challenging
+ There are some novel components such as the lazy updates and implicit leverage score sampling. It is conceivable these might have other applications
+ Brings matrix sketching/randomized linear algebra techniques to the algorithmic discrepancy space
-ves
- Heavily built on Larsen's algorithm / Lovett--Meka random walk and other existing tools from the literature
- The problem might be of narrow interest, even to the ICML audience
Other Comments Or Suggestions: Might be worth adding nnz(A)+n^3 combinatorial bound to Table 1
page 2 - notation V_{l,*} undefined
Could you adopt a single notation to capture both \cal{T}_mat(m,n,k) and \omega(a,b,c)?
page 5 line 223 and on & 234 and on - most of the content seems repeated
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the valuable feedback and for recognizing the novelty, significance, and technical contributions of our work.
### W1: Connection to existing works
While our work indeed builds upon Larsen's algorithm and Lovett–Meka random walk method, we would like to highlight the significant theoretical and algorithmic advances in our work:
- We introduce an innovative implicit leverage-score sampling technique, enabling us to significantly reduce the computational complexity of hereditary projection from Larsen’s original $O(mn^2)$ (or $O(mn^\omega)$ with fast matrix multiplication) to $O(nnz(A)+n^{\omega})$. This improvement is crucial, particularly for sparse input matrices.
- We provide a robust theoretical analysis that carefully manages error accumulation introduced by randomized sketching methods. Such robustness was not previously established and represents a substantial methodological advancement over existing discrepancy minimization frameworks.
- The lazy-update mechanism we introduce to efficiently implement the iterative Edge-Walk algorithm fundamentally reduces computational complexity from Larsen’s $O(mn^2+n^3)$ to our result of $\tilde{O}(nnz(A) + n^{2.53})$. This addresses and overcomes a significant computational barrier identified in prior literature.
### W2: Interest to ICML community
Thanks for pointing this out. We argue that the broad relevance of discrepancy theory to the ICML community stems from its strong connections to central themes in machine learning. Specifically, discrepancy minimization intersects significantly with computational learning theory [1,2], computer vision [3], unsupervised learning [4], attention KV caching [5], differential privacy [6], and sampling [7,8].
More specifically,
[1,2] introduces the relationship of discrepancy and concepts in learning theory such as VC dimension, PAC learning.
[3] introduces a method to learn hash functions via discrepancy minimization. Learning hash functions in content-based image retrieval optimize binary codes to preserve similarity in high-dimensional feature spaces, enabling faster and more efficient image search.
[4] leverage discrepancy minimization for unsupervised graph matching by aligning predictions from classical solvers and neural models.
[5] proposed an algorithm for compressing the KV cache recursively using a geometric correlated sampling process based on discrepancy theory
[6] investigated the relationship between discrepancy minimization and differential privacy in the context of linear queries over histograms.
Quasi-Monte Carlo methods [7,8] leverage concepts from discrepancy theory by employing low-discrepancy sequences to efficiently approximate high-dimensional integrals and expectations.
In the final manuscript, we will explicitly clarify and elaborate on these connections to further emphasize the relevance and significance of our work to the ICML audience.
[1] Matousek, Jiri. Geometric discrepancy: An illustrated guide. 2009
[2] Karnin, Zohar, and Edo Liberty. Discrepancy, coresets, and sketches in machine learning. COLT’19
[3] Chen, Zhixiang, et al. Deep hashing via discrepancy minimization. CVPR’18
[4] Wang, Runzhong, Junchi Yan, and Xiaokang Yang. Unsupervised learning of graph matching with mixture of modes via discrepancy minimization. TPAMI’23
[5] Han, Insu, et al. BalanceKV: KV Cache Compression through Discrepancy Theory. arXiv preprint:2502.07861
[6] Nikolov, Aleksandar, Kunal Talwar, and Li Zhang. The geometry of differential privacy: the sparse and approximate cases. STOC’13.
[7] Lyu, Yueming, Yuan Yuan, and Ivor Tsang. Subgroup-based rank-1 lattice quasi-monte carlo. NeurIPS’20
[8] Lyu, Yueming. Fast rank-1 lattice targeted sampling for black-box optimization. NeurIPS’23
### C1: Adding the combinatorial bound to Table 1
Thank you for your nice suggestion. We will add this to Table 1.
### C2: notation $V_{l,*}$ undefined
Thanks for pointing this out. This means the $l$-th row of the matrix $V$. We will define this in the final manuscript.
### C3: Could you adopt a single notation to capture both \cal{T}_mat(m,n,k) and \omega(a,b,c)?
Thank you for your insightful question. We use two notations intentionally due to their different emphases and contexts: We use $\mathcal{T}_\mathrm{mat}(m,n,k)$ to explicitly highlight absolute matrix dimensions, making it convenient for describing the algorithm's complexity at a high level; meanwhile, $\omega(a,b,c)$ concisely captures relative dimension ratios and is widely adopted in algebraic complexity theory, facilitating rigorous complexity analysis. We will clarify this distinction in our revision to ensure readers fully understand why both notations are necessary and complementary.
### C4: page 5 line 223 and on & 234 and on - most of the content seems repeated
Thanks for pointing this out. We will remove the repeated parts.
We greatly appreciate the positive evaluation of our paper and thank you for your constructive review. | Summary: This paper proposes an improved randomized algorithm for discrepancy minimization problem for real-valued matrices m*nmatrices A with m = poly(n). The paper builds on top of work of Larsen and proposes an improvements to Larsen's algorithm that allow authors to achieve a combinatorial algorithm that runs in input-sparsity time $\widetilde{O}(nnz(A)+n^3)$ with the same approximation guarantee as Larsen's algorithm. The authors also demonstrate how using Fast matrix multiplication one can decrease the runtime to $\widetilde{O}(nnz(A)+n^2.53)$. Prior to this work, the best runtime guarantee in a similar setup was O(mn^2).
The paper introduces novel ideas for each subroutine of the Larsen's algorithm using sketching and score sampling. The authors use sketching techniques to speed up ProjectToSmallRows subroutine of Larsen's algorithm. To overcome $\Omega(n^3)$ barrier for the iterative Partial coloring subroutine authors propose a clever way to perform updates in batches with a new "lookahead" data structure.
Claims And Evidence: The authors provide detailed well-written proofs for the claims made in the paper. They present conceptual arguments and brief summary of the key steps and new ideas compared to the Larsen algorithm in the main text, while detailed definitions and proofs, justifying the claims are presented in the appendix.
Methods And Evaluation Criteria: No experiments are conducted
Theoretical Claims: I skimmed through the proofs and they seem to be sound, but I did not verify the details
Experimental Designs Or Analyses: N/A
Supplementary Material: I skimmed through the proofs in the appendix and they seem to be sound, but I did not verify all the details.
Relation To Broader Scientific Literature: The discrepancy minimization problem has been extensively studied in the literature from both existence (to understand minimal possible discrepancy) and algorithmic perspective. Prior to this work best runtime for the real-valued matrices was by Larsen (2023) running in O(mn^2). This paper focuses on an important practical case of sparse matrices and achieves the first algorithm that works O(nnz(A) +n^3) time providing a significant improvement for tall sparse matrices. This problem was earlier solved by Jain, Sah and Sawhney 2023 for binary matrices, however, their proof does not seem to translate to real-valued matrices easily.
Essential References Not Discussed: In my opinion, the paper provides a very nice overview of the related literature and gives a detailed comparison to the related work.
Other Strengths And Weaknesses: The problem solved in this paper is a well-known problem with multiple applications and a randomized theoretical algorithm with a sub-cubic runtime is definitely of great interest. The paper introduces several new ideas and provides a nice overview of key novelties compared to Larsen's work it builds upon. In my opinion the results are well-presented and easy to read.
Other Comments Or Suggestions: -
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We greatly appreciate the reviewer's recognition of our contributions, specifically, including significant runtime improvements, novel algorithmic techniques, clear comparisons to existing literature, and rigorous theoretical justifications. We believe our contributions represent a significant step forward in improving computational efficiency and advancing algorithmic techniques for discrepancy minimization. Please let us know if you have any further comments regarding our work. Thank you again for your positive feedback. | null | null | null | null | null | null |
AutoAL: Automated Active Learning with Differentiable Query Strategy Search | Accept (poster) | Summary: This paper addresses the active learning problem. Given the existence of numerous active learning methods for selecting the most informative samples, this work proposes an end-to-end framework that integrates multiple approaches. The framework consists of SearchNet and FitNet:
SearchNet assigns a score to each sample, ranks them, and selects those with the highest loss.
FitNet models the data distribution within the unlabeled dataset and guides the training of SearchNet.
However, the main contribution requires further clarification. Instead of selecting a single strategy for the dataset, the framework appears to consider all active learning strategies based on the loss function (Equation 6) and Algorithm 1 (Page 5). If all strategies are incorporated, it is not surprising that the proposed method, AutoAL, achieves the best performance in Figure 2. This suggests that the score definition in Equation 6 is well-designed, but contradicts the claim that the framework selects a single strategy for the dataset.
## update after rebuttal
Additionally, it is unclear whether FitNet is truly necessary. For instance, Line 157 states that FitNet is trained on unlabeled data, whereas Figure 1 indicates that FitNet is trained and fine-tuned using labeled pool data. This inconsistency raises questions about its necessity. Moreover, the ablation study primarily focuses on SearchNet, which appears to play a more significant role in performance and seems to dominate the results.
Claims And Evidence: yes
Methods And Evaluation Criteria: This work proposes a new method that incorporates all active learning algorithms for sample selection.
Theoretical Claims: no theory
Experimental Designs Or Analyses: The experimental design is well-structured. It compares the proposed method with various active learning strategies and includes an ablation study on SearchNet and the active learning candidate strategies. Additionally, experiments are conducted on multiple datasets for each evaluation.
Supplementary Material: no supplementary material
Relation To Broader Scientific Literature: It is particularly interesting for researchers focused on active learning.
Essential References Not Discussed: The work in [1] explores the use of active learning strategies in deep learning networks for question answering. It specifically incorporates uncertainty-based active learning strategies into the training process of question answering models.
[1] Uncertainty-Based Active Learning for Reading Comprehension. Jing Wang, Jie Shen, Xiaofei Ma, and Andrew Arnold. Transactions on Machine Learning Research 2022.
Other Strengths And Weaknesses: If an end-to-end framework could effectively select the best strategy for a given dataset or task, it would be highly interesting. This work is a pioneering effort in that direction.
However, further clarification is needed to demonstrate the necessity of FitNet, as SearchNet alone appears to be sufficient.
Additionally, according to the table, the time cost of the proposed method is relatively low, which is surprising.
Other Comments Or Suggestions: no
Questions For Authors: 1. Is there any optimization strategy used to compute the scores fast, as shown in Table A.1 (Line 565)?
2. Is FitNet truly necessary? Why do the ablation studies not evaluate its impact?
3. Why is FitNet both trained and fine-tuned twice? What is the influence of loss Ls and Lf on the final selection?
4. The experiments focus on classification problems—can the framework also be applied to regression tasks?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank for your feedback and the confirmation of our proposed AutoAL! We agree that AutoAL is an end-to-end framework could effectively select the best strategy for a given dataset or task. We also thank for your valuable question, so we want to clarify the followings:
**Q1:** Is there any optimization strategy used to compute the scores fast, as shown in Table A.1 (Line 565)?
**A1:** This is due to our proposed differential bi-level optimization strategy. Actually all the time cost for AutoAL-Search only contains the training time of the two neural networks. We do find AutoAL may need extra time compared with other baselines, however, the main cost is due to the sample query process of the candidate ALs.
**Q2:** Is FitNet truly necessary? Why do the ablation studies not evaluate its impact?
**A2:** Thanks for pointing out this. Because FitNet is the same net as the final classification net, and is used in AutoAL to yield the informativeness of each unlabeled sample, so we thought it's unnecessary to do ablation on it in our original version. However, we added this experiment on CIFAR100 for you to refer to the results:
| AL Labeled datasets | AutoAL w/o FitNet | AutoAL |
| ------------------- | ----------------- | ---------- |
| 4000 | 33.1 ± 0.2 | 33.2 ± 0.1 |
| 6000 | 36.8 ± 0.2 | 39.4 ± 0.1 |
| 8000 | 40.6 ± 0.1 | 44.1 ± 0.1 |
| 10000 | 41.5 ± 0.2 | 47.2 ± 0.0 |
| 12000 | 45.8 ± 0.3 | 50.4 ± 0.1 |
| 14000 | 47.9 ± 0.2 | 52.5 ± 0.0 |
| 16000 | 50.1 ± 0.1 | 54.9 ± 0.2 |
| 18000 | 49.8 ± 0.3 | 56.1 ± 0.1 |
| 20000 | 53.2 ± 0.1 | 57.0 ± 0.1 |
**Q3:** Why is FitNet both trained and fine-tuned twice? What is the influence of loss Ls and Lf on the final selection?
**A3:** In our settings, FitNet is first trained on the labeled dataset to yield the informativeness of unlabeled sample, then co-optimized with the SearchNet. For $L_s$, it guides the update of SearchNet, to better decide which AL candidate performs the best in the settings now. For $L_f$, it will guide the FitNet to better draw the distribution of unlabeled dataset.
**Q4:** The experiments focus on classification problems—can the framework also be applied to regression tasks?
**A4:** Yes, this is definitely possible. Such as in object detection tasks, as long as the candidate AL strategy can output the most possible coordinates of the target object, AutoAL can learn from it and decide which one is the best coordinate. However, in this paper, we just demonstrate the superior of AutoAL in classification task. We plan to do more tasks as a future work.
**Essential References Not Discussed:** Thanks fo providing the related works. In our initial version, we mainly consider the algorithm selection works with many candidate ALs, but not focused on providing a new AL strategy. However, we believe the works you provided is great and we plan to adds them into our final version. | Summary: The paper proposes an algorithm selection strategy for active learning. The proposed method utilizes the existing labeled dataset and trains differentiable policies for data selection. Experiments are conducted on numerous datasets showing the effectiveness of their algorithm.
Claims And Evidence: I did find the claim in this paper to be unsupported by evidence. This is mostly centered around the comparison against existing algorithm selection algorithms. The authors mention
"[Compared to Hacohen & Weinshall and Zhang et al.], both the computational cost and the lack of differentiability make the optimization of these works inefficient."
I am very confused by this comment as
1. The proposed bilevel optimization approach seems to be much more computational expensive than both of these existing works. Both of the existing works use simple statistics in choosing algorithms, while this paper uses parameterized neural network classes, which is much more computational costly.
2. The author mention the lack of differentiability make existing methods inefficient, but never compare to any of them in experiments. There is also no analysis other than this single sentence.
Methods And Evaluation Criteria: If the authors are trying to make an argument that their methods is better, the author should compare against (Hacohen & Weinshall) and (Zhang et al.), and in their own games. (Hacohen & Weinshall) is proposed for different computation budget settings, and (Zhang et al.) is proposed for imbalance. There is currently no experiment.
Theoretical Claims: N/A
Experimental Designs Or Analyses: See sections above.
Supplementary Material: I did review the computational runtime. There is no comparison against existing work, but the authors claim their method is more efficient. A theoretical time complexity would be helpful here.
Relation To Broader Scientific Literature: This paper studies the algorithm selection work for active learning.
Essential References Not Discussed: I think the paper could benefit from discussing related differentiable policy learning work in active learning. They should also discuss how their parameterization scheme is similar/different from these work.
[1] https://proceedings.neurips.cc/paper_files/paper/2017/file/8ca8da41fe1ebc8d3ca31dc14f5fc56c-Paper.pdf
[2] https://arxiv.org/abs/1909.03585
[3] https://arxiv.org/abs/2010.15382
[4] https://arxiv.org/abs/2108.07670
[5] https://www.jmlr.org/papers/v23/21-0387.html
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: I would recommend the authors position their paper for general active learning scenarios. The two existing literature only study certain scenarios of deep active learning (low-high budget and imbalance). However, I still think it is necessary to compare against these algorithms under their proposed scenarios. If the author's algorithm indeed performs better than those papers in their proposed scenarios, this would be a very influential work. Even if the algorithm does not perform as well, I think the algorithm is still a solid contribution to the community. However, at the same time, the authors also need to note the shortcomings of their approach in such cases.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your valuable feedback. We appreciate that you confirm our contribution to the community on solving the strategy selection problem and our method: using differentiable bi-level framework.
For your concerns, we add more experiments to show the results as below:
**Q1:** The author should compare against (Hacohen & Weinshall) and (Zhang et al.), and in their own games. (Hacohen & Weinshall) is proposed for different computation budget settings, and (Zhang et al.) is proposed for imbalance.
**A1:** We thank for your insightful comments. We do find we should compare with their works so that it can further show the effectiveness of our proposed AutoAL. To compare with [1], we conducted the experiements on two datasets, CIFAR10 and CIFAR100, which are used in both of our experiments and their experiements. In their settings, the CIFAR10 dataset only has two classes and CIFAR100 with 10 classes respectively. The results are shown as follows:
For CIFAR-10:
| AL Labeled datasets | TAILOR | AutoAL |
| ------------------- | ---------- | ---------- |
| 2000 | 80.2 ± 0.2 | 80.2 ± 0.1 |
| 3000 | 84.5 ± 0.1 | 85.3 ± 0.2 |
| 4000 | 87.5 ± 0.2 | 89.4 ± 0.1 |
| 5000 | 89.4 ± 0.2 | 91.7 ± 0.1 |
| 6000 | 91.9 ± 0.2 | 92.8 ± 0.2 |
| 7000 | 93.3 ± 0.1 | 93.5 ± 0.1 |
| 8000 | 95.1 ± 0.1 | 94.8 ± 0.2 |
| 9000 | 96.5 ± 0.2 | 96.6 ± 0.1 |
For CIFAR-100:
| AL Labeled datasets | TAILOR | AutoAL |
| ------------------- | ---------- | ---------- |
| 4000 | 37.8 ± 0.3 | 38.2 ± 0.2 |
| 6000 | 49.8 ± 0.1 | 50.4 ± 0.1 |
| 8000 | 58.2 ± 0.1 | 62.3 ± 0.2 |
| 10000 | 65.8 ± 0.2 | 68.7 ± 0.1 |
| 12000 | 70.9 ± 0.2 | 72.3 ± 0.2 |
| 14000 | 75.5 ± 0.3 | 78.4 ± 0.2 |
| 16000 | 80.0 ± 0.2 | 80.2 ± 0.1 |
| 18000 | 83.2 ± 0.1 | 83.4 ± 0.3 |
We found that AutoAL can outperform TAILOR in nearly all AL iterations, both in CIFAR-10 and CIFAR-100, this result is consistent with the results shown before because for SVHN and other medical datsets, although they are imbalanced, AutoAL can still outperform the baselines.
For [2], unfortunately they didn't open-source their code, but we found a toolbox from [3] which officially implemented Probcover [4] and TypiClust [3], two baselines used in [2]. From the experiment results in [2], we observed that Probcover consistently performs best in low budget settings while Badge [5] excels in high budget settings. Therefore, we selected Probcover, TypiClust, and Badge as our baseline methods, focusing our tests on CIFAR-10.
As shown in our results, AutoAL performs well in medium and high budget settings but underperforms in low budget scenarios. We attribute this to deep neural networks typically requiring larger datasets for proper training—when the budget is low, SearchNet and FitNet cannot be fully optimized. However, traditional AL settings rarely use extremely low budgets, and AutoAL demonstrates its effectiveness when the budget is adequate. We acknowledge that AutoAL is designed for general active learning scenarios, not specifically for low-budget settings.
| Budget (L+A) | 500+500 | 7k+1k | 20k+5k |
| ------------ | ---------- | ---------- | ---------- |
| ProbCover | 50.3 ± 0.4 | 79.8 ± 0.2 | 87.5 ± 0.2 |
| TypiClust | 49.8 ± 0.3 | 80.0 ± 0.2 | 87.2 ± 0.1 |
| Badge | 50.2 ± 0.4 | 79.9 ± 0.1 | 88.1 ± 0.3 |
| AutoAL | 46.8 ± 0.3 | 80.3 ± 0.1 | 89.3 ± 0.1 |
**Essential References Not Discussed:** Thanks for providing the related works. In our initial version, we mainly consider the algorithm selection works with many candidate ALs, but not focused on providing a new AL strategy. However, we believe the works you provided is great and we plan to adds them into our final version.
We hope these results can address your problems, and reconsider our contributions. We appreciate if you can consider raising your score.
**References:**
[1] Zhang, Jifan, et al. "Algorithm selection for deep active learning with imbalanced datasets." Advances in Neural Information Processing Systems 36 (2023): 9614-9647.
[2] Hacohen, Guy, and Daphna Weinshall. "How to select which active learning strategy is best suited for your specific problem and budget." Advances in Neural Information Processing Systems 36 (2023): 13395-13407.
[3] Hacohen, Guy, Avihu Dekel, and Daphna Weinshall. "Active learning on a budget: Opposite strategies suit high and low budgets." arXiv preprint arXiv:2202.02794 (2022).
[4] Yehuda, Ofer, et al. "Active learning through a covering lens." Advances in Neural Information Processing Systems 35 (2022): 22354-22367.
[5] Ash, Jordan T., et al. "Deep batch active learning by diverse, uncertain gradient lower bounds." arXiv preprint arXiv:1906.03671 (2019).
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal and I have raised my scores.
---
Reply to Comment 1.1.1:
Comment: Thanks for your score and response. Also appreciate your time and efforts on reviewing our work. | Summary: This paper addresses the challenge of active learning (AL) by proposing AutoAL, a automated active learning framework. The authors highlight that optimal AL strategies vary across different datasets and problem settings. To address this, AutoAL first extracts scores from multiple acquisition functions and then employs a bi-level optimization approach to identify the most effective acquisition strategy dynamically. The model consists of FitNet and SearchNet, which are trained in a differentiable framework. Specifically, the labeled dataset is partitioned into a pseudo-validation set and a training set, enabling FitNet to fit the training set while SearchNet determines the most informative unlabeled samples for annotation.
Claims And Evidence: 1. First Differentiable AL Strategy Selection
- To the best of my knowledge, AutoAL is the first differentiable active learning selection method. The use of bi-level optimization for acquisition function selection has been explored in other fields, such as few-shot learning, but it has not been explicitly applied in AL before.
- The paper provides empirical evidence across multiple datasets showing that AutoAL consistently outperforms prior AL methods.
2. Assumption on Sampling Bias in Labeled Data
- AutoAL assumes that dividing the labeled set into two subsets can sufficiently approximate the data distribution of the unlabeled pool (Line 173 - 178).
- However, active learning is inherently biased, as sampling bias exists in the labeled data [Farquhar’21]. The assumption that the sampled labeled data follows the original data distribution does not hold, which could affect the performance of AutoAL. (See discussion under "Methods And Evaluation Criteria.")
3. Baseline Implementation Concerns
- The result shows performance gains across most datasets, but there are concerns about whether the baselines were correctly implemented.
- Some prior AL studies indicate that performance may degrade as AL rounds progress, which is observed in Figure 2, particularly for PathMNIST.
[Farquhar’21] Farquhar, S., Gal, Y., & Rainforth, T. (2021). On statistical bias in active learning: How and when to fix it. ICML21
Methods And Evaluation Criteria: 1. Sampling Bias in Actively Selected Data
- One major issue with AutoAL is that actively sampled data does not follow the same distribution as the unlabeled pool.
- Farquhar et al. (2021) demonstrated that actively sampled data has inherent statistical biases, meaning FitNet and SearchNet do not necessarily generalize well to the full data distribution.
- Moreover, since the labeled dataset is halved for training FitNet and SearchNet, this could further change the optimal AL strategy, leading to unexpected selection behaviors.
2. Other Methodological Concerns
- Apart from the issue mentioned above, the design of AutoAL's framework and its evaluation metrics appear reasonable.
[Farquhar’21] Farquhar, S., Gal, Y., & Rainforth, T. (2021). On statistical bias in active learning: How and when to fix it. ICML21
Theoretical Claims: This work does not introduce new theoretical claims.
Experimental Designs Or Analyses: 1. Potential Issues in Baseline Comparisons
- In Figure 2, several baseline methods show performance degradation in later rounds, which is unexpected.
- This issue is particularly severe in PathMNIST, where adding more labeled data results in worse accuracy.
- Given that the experiments were conducted with three trials and reported variance, such trends contradict intuition.
- There is a concern that some baselines may not have been properly implemented, which could unfairly favor AutoAL.
2. Ablation Studies Provide Useful Insights
- Figure 4 (Candidate set size ablation) and Figure 5 (AL strategy score visualization) provide useful explanations regarding how AutoAL selects acquisition strategies dynamically.
- The ablation design is clear and informative.
Supplementary Material: Yes, all supplementary material was reviewed.
Relation To Broader Scientific Literature: 1. AutoAL aligns with prior studies that show the best AL strategy depends on budget and dataset properties.
2. Bi-level optimization has been applied in few-shot learning and hyperparameter tuning, but this is the first work to introduce differentiability into AL strategy search.
Essential References Not Discussed: Some recent active learning methods [Mahmood’21, Kim’23, Yehuda’22] are missing. Considering the problem setting [Hacohen’22] needs to be included.
[Mahmood’21] Mahmood, R., Fidler, S., & Law, M. T. (2021). Low budget active learning via Wasserstein distance: An integer programming approach. ICLR 2022.
[Yehuda’22] Yehuda, O., Dekel, A., Hacohen, G., & Weinshall, D. (2022). Active learning through a covering lens. NeurIPS 2022.
[Kim’23] Kim, Y. Y., Cho, Y., Jang, J., Na, B., Kim, Y., Song, K., ... & Moon, I. C. (2023, July). SAAL: Sharpness-aware active learning. In ICML 2023.
[Hacohen’22] Hacohen, G., Dekel, A., & Weinshall, D. (2022). Active learning on a budget: Opposite strategies suit high and low budgets. In ICML 2022.
Other Strengths And Weaknesses: 1. Clarity Issues in Writing and Notation
- The notation is difficult to follow, and the mathematical expressions are not clearly defined.
- For example, the inputs and outputs of SearchNet and FitNet (Lines 165 - 178) are not explicitly defined, making the method difficult to understand.
- Some notations are used before being defined (e.g., Equation (1) loss terms are not introduced until Equations (7) and (8)). Some notation in Equation (5) is not defined.
- Figure 1 is difficult to interpret, as it reuses model illustration with "After Training" arrow without clear explanations.
2. High Computational Cost
- AutoAL requires training two networks and running R inner-loop updates.
- According to Table 2, AutoAL is up to 7x more expensive than entropy-based sampling.
- The paper does not analyze the algorithmic complexity, making it difficult to assess scalability to large-scale datasets like ImageNet.
Other Comments Or Suggestions: None
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your feedback. For your questions, we make the following comments to clarify our points:
**Q1:** **Sampling Bias in Actively Selected Data**
**A1:** For our initial seed dataset setting, it is i.i.d., ensuring an unbiased starting point. Traditional single-criterion AL strategies, especially those based solely on uncertainty [1], are more susceptible to accumulating such bias over iterations. In contrast, AutoAL integrates multiple AL strategies, each contributing different perspectives (uncertainty, diversity, etc.). This fusion, combining multiple AL candidates while maintaining a differentiable framework between search and fit nets, inherently reduces bias, prevents overfitting to any individual AL sampling strategy, and adapts dynamically as the AL process evolves.
**Q2: Baseline implementation Issue**
**A2:** Thanks for the question. We observed this problem too. To clarify, all baseline implementations come from public GitHub repositories, not from our own. Our framework builds upon the open-source deepAL [1]. The accuracy degradation appears in many works, including Figure 1 in [3,4], Figure 3(b) in [5], Figure 3 and 4 in [6], and deepAL [1]. We attribute this to two factors:
1) The amount of data causing overfitting in the classification model.
2) Medical datasets often contain redundancy and confusing information. These medical images have many-to-one relationships, as one patient may correspond to several pathology images. Some patients may have multiple conditions (e.g., X-rays showing posterior spinal fixators used for spine repair). These features can influence predictions. Proper diagnosis requires both local and global features, making bias problems more severe in these cases.
**Q3: Writing Issues**
**Q3.1:** Notion Issues.
**A3.1:** We are sorry that there are many notations in our method parts. We will make a table in the appendix to define the important notions.
We tried to describe the input for SearchNet and Fitnet in Figure 1. The initialed labeled pool is divided to two queues. The first queue is used to train FitNet. The second queue is used to train both FitNet and SearchNet. Thanks for pointing out, we will polish the writing in our final version.
**Q3.2:** Notions used before defined.
**A3.2:** Our writing logic was to first interpret the whole framework of AutoAL, then the detailed parts such as the loss functions in Equation (1).
**Q3.3:** Figure 1.
**A3.3:** AutoAL's FitNet is first trained on the first queue of labeled dataset. After the parameter of FitNet is adapted to the second training step, FitNet and SearchNet are jointly trained with the second data queue. We will add more explanation to the description in Figure 1.
**Q4: Runtime Complexity**
**A4:** Please first refer to the rebuttal to **Reviewer khE5, A2**. Follow the part 5.1 of pulished work [7], we made a similar complexity analysis. As described in our appendix A.1. let $N_{search}$ denotes the updating time of SearchNet and FitNet in each AL round per batch, $N_{train}$ denotes the sample querying and classification model training in each AL round per batch. We can define the AL score querying time for each candidate AL per batch as $Q_{i}$. When there are $M$ AL algorithms, in each batch, the computation complexity is O(T$\sum_{b=1}^{B_{max}}(N_{search}+N_{train}+\sum_{i=1}^{M}Q_{i})$) in the worst case, where T is the total number of rounds and $B_{max}$ is the number of batches depending on the stop criterion of AL. In the future, we plan to do parallel processing for the candidate AL score calculation, which will further improve the upper bound to O(T$\sum_{b=1}^{B_{max}}(N_{search}+N_{train}+Q_{imax}$))
**Q5: Essential References Not Discussed**
**A5:** Thanks for finding these. About the low budget and high budget setting, we have added new experiments to show the results. Please refer to the reply to **Reviewer bNSN.**
We hope you can reconsider the final rating.
**Reference:**
[1] Sharma, Manali, and Mustafa Bilgic. "Evidence-based uncertainty sampling for active learning." Data Mining and Knowledge Discovery 31 (2017): 164-202.
[2] Zhan, Xueying, et al. "A comparative survey of deep active learning." arXiv preprint arXiv:2203.13450 (2022).
[3] Gal, Yarin, Riashat Islam, and Zoubin Ghahramani. "Deep bayesian active learning with image data." International conference on machine learning. PMLR, 2017.
[4] Geifman, Yonatan, and Ran El-Yaniv. "Deep active learning over the long tail." arXiv preprint arXiv:1711.00941 (2017).
[5] Kim, Seong Tae, Farrukh Mushtaq, and Nassir Navab. "Confident coreset for active learning in medical image analysis." arXiv preprint arXiv:2004.02200 (2020).
[6] Mishal, Inbal, and Daphna Weinshall. "DCoM: Active Learning for All Learners." arXiv preprint arXiv:2407.01804 (2024).
[7] Zhang, Jifan, et al. "Algorithm selection for deep active learning with imbalanced datasets." Advances in Neural Information Processing Systems 36 (2023): 9614-9647. | Summary: The proposed AutoAL is an automatic query strategy search algorithm that utilizes bi-level optimization framework to select optimal AL strategies built upon existing uncertainty and diversity-based approaches.
Claims And Evidence: Yes, most of the claims are supported by clear and convincing evidence. The computational overhead is not very convincing considering the performance the proposed method delivers.
Methods And Evaluation Criteria: Yes, several baselines are explored with a range of well-known datasets.
Theoretical Claims: The theoretical claims look fine to me. The differentiable query strategy optimization, the bi-level optimization problem setup look reasonable.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes. The complexity analysis and class imbalance information are helpful to understand the contribution.
Relation To Broader Scientific Literature: AutoML is basically an automatic query search algorithm which may help in selecting the optimal AL strategies for various applications.
Essential References Not Discussed: 1. Desreumaux, L., & Lemaire, V. (2020). Learning active learning at the crossroads? Evaluation and discussion. arXiv preprint arXiv:2012.09631.
2. Fang, M., Li, Y., & Cohn, T. (2017). Learning how to active learn: A deep reinforcement learning approach. arXiv preprint arXiv:1708.02383.
3. Makili, L. E., Vega Sánchez, J. A., & Dormido-Canto, S. Active learning using conformal predictors: Application to image classification.
The approaches in these papers are somewhat similar to the proposed method. These papers could have been used as part of the baselines or references.
Other Strengths And Weaknesses: Strengths –
The proposed framework AutoAL designed on top of uncertainty and diversity based AL approaches, utilizes two neural networks optimized concurrently under bi-level optimization framework to select optimal AL strategies to solve the traditional active learning problem. Overall, the performance looks promising and the paper is easy to follow.
Weaknesses -
The proposed AutoAL does not seem novel . It utilizes the same uncertainty and diversity-based criterion to select batches of samples.
The average run time of the total AutoAL is significantly higher than most of the baselines used as part of the experiments, perhaps because of the involvement of deep neural nets, SearchNet and FitNet co-optimization in a bi-level optimization structure, whereas the accuracy is relatively 1%-3% better than most of the baselines.
It is not clear how AutoAL could be used to add more AL frameworks to extend its applications to other domains such as image segmentation, object detection etc.
Other Comments Or Suggestions: It would be interesting to see how vision transformer models would work based on this framework.
Questions For Authors: Please answer the concerns in the weaknesses section.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: hank you for your valuable feedback. We appreciate that you confirm our method development, promising performance, and fluent paper writing.
For your concerns, we make the following comments to clarify our points:
**Essential References Not Discussed:** We thank for your efforts in finding these related materials for us. We plan to add them to the related works. Especially for [1], it contains a lot of datasets, which worth trying.
We plan to add one sentence to related works part, in *adaptive sample selection in AL* section, [1] frame the algorithm selection task as "learning how to actively learn" and use deep Q-learning algorithm to select which strategy is best suited.
**Q1:** The proposed AutoAL does not seem novel. It utilizes the same uncertainty and diversity-based criterion to select batches of samples.
**A1:** Our contribution creates a differentiable bridge connecting "search" and "fit" models in Active Learning, outperforming manual and non-differentiable approaches. While AutoAL builds on existing uncertainty and diversity-based methods, it solves two key problems:
1) Single-criterion AL methods accumulate bias over iterations. AutoAL incorporates multiple methods to reduce this bias.
2) Criteria that work well in current settings may perform bad in future rounds. For example, BADGE [3] performs poorly with low budgets but excels with increased resources. AutoAL selects the optimal criterion each round to address this issue.
This integration reduces cumulative bias, with experiments confirming AutoAL outperforms two-stage selection methods like BADGE [3].
**Q2:** The average run time of the total AutoAL is significantly higher than most of the baselines used as part of the experiments, perhaps because of the involvement of deep neural nets, SearchNet and FitNet co-optimization in a bi-level optimization structure, whereas the accuracy is relatively 1%-3% better than most of the baselines.
**A2:** Thanks for pointing out the average runtime issue. Please refer to Appendix A.1, where we divided the total runtime into three main parts. The co-optimization runtime is relatively small compared to the time that candidate ALs spend querying scores for images. We believe this cost is acceptable. Our tests used 7 candidate ALs, which isn't always necessary (as shown in Figure 4 for OrganCMNIST). Using fewer candidates would significantly reduce runtime. We plan to integrate AL methods with lower computational complexity to further reduce AutoAL's total runtime.
**Q3:** It is not clear how AutoAL could be used to add more AL frameworks to extend its applications to other domains such as image segmentation, object detection etc.
**A3:** Thanks for your feedback. We plan to test AutoAL on various applications, as our method is task-agnostic. For tasks like image segmentation, whenever candidate AL methods [4,5] can score instances, SearchNet and FitNet will train on these scores. Since most published works [2,6] also only focus on image classification datasets, we believe our results demonstrate AutoAL's superiority in most scenarios.
**Q4:** It would be interesting to see how vision transformer models would work based on this framework.
**A4:** Thanks for your feedback. We want to clarify that using a basic learning is a normal setting which has been used in published works [1,4], however, we plan to add the experiments for transformers in the future to see the performance of AutoAL [6,7].
**Reference:**
[1] Desreumaux, Louis, and Vincent Lemaire. "Learning active learning at the crossroads? evaluation and discussion." arXiv preprint arXiv:2012.09631 (2020).
[2] Hacohen, Guy, and Daphna Weinshall. "How to select which active learning strategy is best suited for your specific problem and budget." Advances in Neural Information Processing Systems 36 (2023): 13395-13407.
[3] Ash, Jordan T., et al. "Deep batch active learning by diverse, uncertain gradient lower bounds." arXiv preprint arXiv:1906.03671 (2019).
[4] Li, Jun, José M. Bioucas-Dias, and Antonio Plaza. "Hyperspectral image segmentation using a new Bayesian approach with active learning." IEEE Transactions on Geoscience and Remote Sensing 49.10 (2011): 3947-3960.
[5] Yang, Lin, et al. "Suggestive annotation: A deep active learning framework for biomedical image segmentation." Medical Image Computing and Computer Assisted Intervention− MICCAI 2017: 20th International Conference, Quebec City, QC, Canada, September 11-13, 2017, Proceedings, Part III 20. Springer International Publishing, 2017.
[6] Sener, Ozan, and Silvio Savarese. "Active learning for convolutional neural networks: A core-set approach." arXiv preprint arXiv:1708.00489 (2017).
[7] Yoo, Donggeun, and In So Kweon. "Learning loss for active learning." Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2019. | Summary: This paper proposes a new method for active selection that leverages existing AL algorithms as constituent agents. It consists of two neural networks, fitnet and searchnet, each trained using the pool of data that has already been labeled. searchnet is fit to select the best ament a set of pre-chosen active learning algorithms, and fitnet, which is used to judge the usefulness of each unlabeled samples and helps guide searchnet. The two are trained in a bilevel optimization framework that’s partly enabled by some additional machinery that makes the learning objective for both models differentiable. The fully trained models are used to guide data selection.
Claims And Evidence: The authors claim that this is an effective approach to data selection, and they provide experiments on image data demonstrating that this seems to be the case.
Methods And Evaluation Criteria: The criteria make sense for the problem at hand, but it would have been nice to have seen more variance in the model architecture (they just used resnets), batch size, and data type (currently just images).
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The experimental design is typical for pool-based active learning, consisting of labeled data, unlabeled data, and a sequential learning algorithm. The agent selects unlabeled points it believes are most productive for learning, they're labeled by an oracle, placed in the labeled pool, and the classifier is updated. The goal is to have the highest performing model possible given a fixed labeling budget.
Supplementary Material: The supplement only contains some additional experimental details—I looked through it but didn't think it needed to be included.
Relation To Broader Scientific Literature: The key contribution is in a straightforward and effective way to do unlabeled data selection in a fashion that aggregates existing method. Such an approach can be expensive, as the constituent algorithms can be expensive on their own, but I believe there is a growing need for effective data selection strategies.
Essential References Not Discussed: Active learning is a very large field, and people have been thinking about it for a long time, but I think limiting the related work to the few mentioned contemporary papers to be acceptable. I wouldn't say anything truly essential has been omitted.
Other Strengths And Weaknesses: The provided results seem compelling, but here are a few notes that I feel would make the paper stronger:
- Experiments are only done on image data and with resnets. I wonder how contingent the performance of the approach is on the convolution inductive bias—it would be useful to see some experiments with more naive models, like MLPs. Along these lines, I’ve seen other papers show results for different acquisition batch sizes, which I feel would also give more clarity to how the approach performs.
- Experiments only show the earliest parts of learning curves. The results look very promising, but it would be nice to see asymptotic performance.
Other Comments Or Suggestions: This is a weak point, but calling the method AutoAL seems very general, as other techniques, such as ALBL, also do what I think I’d classify superficially as “automated active learning” in the same way. I'd consider switching to something more descriptive of this technique in particular.
Questions For Authors: As mentioned above, questions are around the robustness of the approach to other data types, batch sizes, and model architectures.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your valuable comments and time. We appreciate that you confirm our contribution and appreciate our work.
For your questions, we add more experiment results for your reference:
**Q1:** Experiments are only done on image data and with resnets. I wonder how contingent the performance of the approach is on the convolution inductive bias—it would be useful to see some experiments with more naive models, like MLPs. Along these lines, I’ve seen other papers show results for different acquisition batch sizes, which I feel would also give more clarity to how the approach performs.
**Q2:** Experiments only show the earliest parts of learning curves. The results look very promising, but it would be nice to see asymptotic performance.
**A1 and A2:** To answer your questions, we conduct new experiments to show the results, especially on CIFAR10 dataset, as it's commonly used by other related works [1,2]. Speicially, we changed the acquisition batch size from 1000 (original setting of our paper) to 5000 to show the difference. Then we compare the results between our proposed AutoAL with two baselines, KMeansSampling [3] and LPL [4], which are the worst and best performed baseline in our original CIFAR 10 experiments. The results show that our method can still outperform the baselines. Also using a basic learning is a normal setting which has been used in published works [1,4], but we plan to add the experiments for MLPs in the future.
| Labeled dataset | KMeansSampling | LPL | AutoAL |
| --------------- | -------------- | ---------- | ---------- |
| 10000 | 74.3 ± 0.1 | 72.6 ± 0.2 | 74.2± 0.1 |
| 15000 | 77.2 ± 0.1 | 78.7 ± 0.1 | 78.8 ± 0.1 |
| 20000 | 80.4 ± 0.0 | 82.2 ± 0.1 | 82.7 ± 0.0 |
| 25000 | 82.3 ± 0.1 | 85.0 ± 0.2 | 85.3 ± 0.1 |
| 30000 | 84.2 ± 0.1 | 87.8 ± 0.1 | 88.4 ± 0.1 |
| 35000 | 85.6 ± 0.2 | 88.6 ± 0.2 | 89.3 ± 0.1 |
| 40000 | 86.1 ± 0.1 | 89.8 ± 0.1 | 90.6 ± 0.0 |
**Q3:** This is a weak point, but calling the method AutoAL seems very general, as other techniques, such as ALBL, also do what I think I’d classify superficially as “automated active learning” in the same way. I'd consider switching to something more descriptive of this technique in particular.
**A3:** Thanks for your suggestions. We plan to change the name AutoAL to DDAL, representing **D**ifferentiable **D**eep **A**ctive **L**earning in the final version.
**References:**
[1] Sener, Ozan, and Silvio Savarese. "Active learning for convolutional neural networks: A core-set approach." arXiv preprint arXiv:1708.00489 (2017).
[2] Hacohen, Guy, and Daphna Weinshall. "How to select which active learning strategy is best suited for your specific problem and budget." Advances in Neural Information Processing Systems 36 (2023): 13395-13407.
[3] Ahmed, Mohiuddin, Raihan Seraj, and Syed Mohammed Shamsul Islam. "The k-means algorithm: A comprehensive survey and performance evaluation." Electronics 9.8 (2020): 1295.
[4] Yoo, Donggeun, and In So Kweon. "Learning loss for active learning." Proceedings of the IEEE/CVF conference on computer vision and pattern recognition. 2019. | null | null | null | null |
Just Enough Shifts: Mitigating Over-Refusal in Aligned Language Models with Targeted Representation Fine-Tuning | Accept (poster) | Summary: This paper addresses the over-refusal problem in aligned LLMs that unnecessarily reject benign user prompts. The authors identify specific layers whose latent representations best distinguish between benign and malicious prompts, then selectively adjust embeddings to move prompts "just enough" from rejection to acceptance. Their approach uses a proxy that measures refusal contribution through query projection onto the refusal vector, deriving the shift from a locally linear approximation of the refusal boundary. Experiments across three models demonstrate higher compliance rates than fine-tuning while maintaining safety scores and general functionality.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: The paper mitigates the over-refusal issue of LLMs while maintaining a high safety score and general capability, enhancing the usability of LLMs.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strength:
1. One of the key novelties of this paper lies in the proposal of "just enough" shift. The paper gives one motivation as uniform shift leads to gebbrish generation.
2. The method targets specific layers for adjustment rather than modifying the entire model, requires minimal compute compared to full model retraining
3. Results show improved compliance rates compared to fine-tuning approaches while maintaining safety scores and general model functionality
Weakness:
1. The proposed method is not applicable to black-box models.
2. The generalization of the learned shift remains untested. Training on some datasets and evaluating on non-overlapping datasets would provide insight into its robustness.
3. The evaluation is limited in scope—only two architectures are tested, and activation-based baselines are only evaluated on one model.
Other Comments Or Suggestions: The presentation can be improved. For example, in Figure 1, there is too much space inside the quote box and the text is not centered.
Questions For Authors: 1. Can you clarify what you mean by pseudo-harmful prompts?
2. How does the learned shift generalize to unseen datasets? Have you considered training on some datasets and evaluating on others?
3. Why were activation-based baselines evaluated on only one model? Would broader comparisons strengthen the claims?
4. Given that the method is not applicable to black-box models, do you see potential adaptations that could make it usable in such settings?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback. We have provided our responses below, and we hope they clarify the points you raised. If our responses have adequately addressed your initial concerns, we would be grateful if you would consider adjusting your evaluation accordingly.
## (A)
We define pseudo-harmful prompts in line 39 of the Introduction- they are queries which appear potentially harmful but are benign in nature.
## (B)
We address the question of generalization to unseen datasets through our experimental setup. We train our model on 25 examples each from XSTest, Scope, ORBench, and PHTest, and then evaluate on the corresponding held-out partitions of those datasets. In addition, we include OKTest as an entirely unseen benchmark to assess how well our learned shift extends beyond the trained domains. The results are summarized in Table 1.
To further address concerns about out-of-domain generalization, we also conduct a supplementary experiment in which training is restricted to only 25 queries from XSTest and ORBench along with the harmful and harmless queries from Hexphi and UltraChat. As shown in the experiments below, the model retains its out-of-distribution (OOD) robustness even when we vary the over-refusal distributions used during training.
| Method | XS Test CR (In-Dist) | SCOPE CR (OOD)| Orbench CR (OOD)| Phtest CR (OOD)| OKTest CR (OOD)| Avg OR Compliance Rate| Advbench Safety Score| Tradeoff Score |
|-|-|-|-|-|-|-|-|-|
| ACTOR (25 XS Test) | 96.00| 90.39| 73.09| 95.03| 94.00| 89.70| 99.03| 94.37 |
| Method | XS Test CR (OOD)| SCOPE CR(OOD)| Orbench CR (In-Dist)| Phtest CR(OOD)| OKTest CR (OOD) | Avg OR Compliance Rate| Advbench Safety Score| Tradeoff Score |
|-|-|-|-|-|-|-|-|-|
| ACTOR (25 ORB-H) | 94.67| 90.73| 73.91| 96.05| 94.33| 89.94| 98.85| 94.40 |
## (C)
We agree that broader comparisons can further strengthen our work. We have now incorporated comparisons against multiple baselines. First, we present the following table discussing the features of all existing approaches and their comparison with ACTOR.
| Method| Mitigation of Over-Refusal | Train Time/ Inference Time | Robustness |
|-|-|-|-|
| Self-CD| High| **Inference Time** - Requires 2 generations for the same input | -|
| DRO| Poor| **Train Time** - Introduces external parameters | -|
| Safety Patching| High | **Train Time** - Requires training twice| - |
| Safe-Decoding| Poor | **Train Time** - Requires 2 generations for the same input | -|
| SCANS| High| Inference Time| Low|
| Surgical| High| Inference Time| Low |
| ACTOR| High| Train Time | High|
1. **Results for Llama-2-7b-chat-hf**
| Method| XS Test CR | SCOPE CR| Orbench CR | Phtest CR| OKTest CR) | Avg OR CR | Advbench SS | Tradeoff Score |
|--|-|-|-|-|-|-|-|-|
| Default| 80 | 52.61| 29.45 | 69.6 | 76 | 61.53 | 99.62| 80.58|
| Safe-Decoding | 29.12| 15.32 | 7.45 | 26.03 | 45.24 | 24.63 | 100 | 62.32 |
| DRO| 58 | 21.25 | 14.11 | 62.22 | 76 | 46.32| 100| 73.16|
| Self CD| 90.67| 80.94| 61.94| 87.41| 92| 82.59| 95.77| 89.18|
| SCANs| 95.33| 76.72| 40.52| 90.44| 99 | 80.40| 99.23| 89.82|
| Surgical | 90.67| 89.38| 69.16| 93.42| 89.33| 86.39| 99.42| 92.90 |
| Ours| 95.33| 91.57| 76.28| 96.86| 93.67 | **90.74** |99.03| **94.88**|
2. **Results for Gemma-7b-it**
| Method| XS Test CR | SCOPE CR | Orbench CR | Phtest CR| OKTest CR | Avg OR CR | Advbench SS | Tradeoff Score |
|-|-|---|--|--|-|--|--|-|
| Default | 72.01| 58.18 | 65.71 | 88.92 | 74.00 | 71.76 | 94.00 | 82.88 |
| Safe-Decoding | 32.12| 19.43 | 8.32| 38.21 | 40.34| 27.68| 98.32| 63.00|
| DRO| 52.04| 44.92| 58.39| 75.01| 71.28| 60.33| 97.78| 79.06 |
| Self CD| 78.00| 64.75| 74.20| 88.08| 73.00| 75.61| 87.12 | 81.36|
| SCANs | 56.66 | 56.15| 70.87| 80.12| 53.66| 63.49 | 93.65| 78.57|
| Surgical| 76.67 | 61.20 | 74.20 | 89.72| 76.33 | 75.62| 90.96| 83.29|
| Ours| 79.33 | 62.73| 73.83| 91.15| 78.00| **77.01**| 92.5| **84.75**|
Our results continue to show that ACTOR outperforms these broader baselines in reducing over-refusals while maintaining safety scores.
## (D)
We acknowledge that our approach relies on access to model internals, which may be unavailable for users of closed-source or black-box systems. However, we do not view this as a fundamental limitation. In practice, closed-source model developers do have full access to these internals and can adopt our method if they choose. Moreover, the ability to examine the model’s internal representation space provides critical insights for understanding and mitigating over-refusals—insights that purely API-level or prompt-based methods cannot readily capture. | Summary: The paper proposes a fine-tuning based method to solve the over-refusal problem encountered by many LLMs. The method first tries to extract an over-refusal vector from the models using different prompts and then it tries to steer the model towards the embedding as defined in equation 9. The overall performance is strong as measured on various benchmarks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: The theoretical claim is not rigorous since the problem cannot be exactly defined. Thus most of the conclusion in the paper is empirical.
Experimental Designs Or Analyses: Yes, the experiment design is valid.
Supplementary Material: Yes, I looked through the supplementary material such as the algorithm and some further discussions.
Relation To Broader Scientific Literature: The paper contributes a method to greatly reduce the over-refusal behaviors without affect its original performance. So it will be generally useful to trading off between being safe and helpful.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: ## Strength
1. The paper is well written and easy to follow
2. The proposed method is simple and effective
3. After fine-tuning, the model's original performance is well-preserved.
## Weakness
1. the proposed method is very close to [1] except with a fine-tuning stage, this makes the contribution less significant. And [1] is not discussed extensively in the work.
2. lack of comparison with baselines, although SafeDecoding or DRO may show lower performances, but it's better to have them in the table for comparison. Are they better or worse than SFT?
3. lack of ablation study on the number of calibration samples, how is 210 and 25 selected for the training dataset, how does it affect the downstream performances if you change them?
4. all the results are reported at a high level, but most benchmarks have provided specific categories for refusal. what are the performance on specific categories in the benchmarks. Currently there doesn't seem to be such analysis
[1] Surgical, Cheap, and Flexible: Mitigating False Refusal in Language Models via Single Vector Ablation
Other Comments Or Suggestions: N/A
Questions For Authors: 1. can the author explain the difference between the current work and [1], looks like it's built upon [1] with a little bit fine-tuning.
[1] Surgical, Cheap, and Flexible: Mitigating False Refusal in Language Models via Single Vector Ablation
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback. We have provided our responses below, and we hope they clarify the points you raised. If our responses have adequately addressed your initial concerns, we would be grateful if you would consider adjusting your evaluation accordingly.
## (A)
Our approach differs fundamentally from the single‐vector “surgical” method [1], which computes a “false‐refusal” vector from a set of harmless, harmful, and pseudo‐harmful queries. We observe that simply switching the pseudo‐harmful dataset from ORB-H to OKTest led to substantial fluctuations in performance.
| Method | OR Compliance Rate |
|-|-|
| Surgical (ORB-H) | 86.39 |
| Surgical (OKTest) | 63.88 |
These fluctuations arise because the method bakes a **single fixed vector** directly into the model’s weights and applies it uniformly to every query—a “one‐size‐fits‐all” mechanism. Consequently, the model’s efficacy heavily depends on the specific distribution from which the vector is extracted, rendering it brittle under distributional shifts. shifts. We explore a natural extension of this approach in the fine‐tuning setting under the subsubsection “Would Uniform Shifts Work?” (Sec 3.2). We show that a single uniform vector shift leads to **destructive fine‐tuning**, with more discussion in Appendix B.
Instead of a single fixed vector, ACTOR repeatedly updates both the model parameters and the refusal direction during fine‐tuning. Mathematically, rather than enforcing a constant scaling factor, ACTOR’s loss function promotes an **“individualized” or “just enough” shift**—proportional to each query’s **projection onto the refusal direction**—so that the model can adapt its internal representation on a query‐by‐query basis via **minimal intervention**. We discuss these design choices in more detail in Section 3. This iterative, dynamic mechanism makes ACTOR **robust**: instead of relying on a single axis of correction, it exploits the full capacity of the model’s internal activation space to handle diverse data distributions.
To further validate this robustness, we computed the initial refusal direction for ACTOR using three different harmful data distributions as shown in Fig 5 (Sec 4.2) and the table below. ACTOR consistently **maintains strong performance**, even when the refusal direction is computed from different data sources.
| Datasets Used for Refusal Direction | Method | Avg OR Compliance Rate |Advbench Safety Score|
|--|-|-|-|
| D_harmful = Hexphi | ACTOR | 90.01 | 99.03 |
| D_harmful = BeaverTails | ACTOR | 89.84| 98.95 |
| D_harmful = Malicious| ACTOR | 89.94 | 98.85 |
We hope this clarifies why our method is not merely an extension of [1] augmented with fine‐tuning. Our design deliberately addresses the pitfalls of a single‐vector solution and provides a more adaptive, reliable alignment strategy.
## (B)
**Baselines**- Kindly refer to our rebuttal to Reviewer eEU9 (C). Both SafeDecoding and DRO suffer from a major over-refusal problem and perform worse than SFT.
## (C)
The 210 benign examples are randomly sampled from the 7 categories of the UltraChat Dataset (n=30). The 25 queries from XSTest, SCOPE, OR-Bench-Hard-1k, PhTest benchmarks are also sampled randomly with their held-out versions used for evaluation and OKTest serving as an OOD dataset.
We experiment with 2 additional settings where we set **n=15 and 50** for UltraChat-
| Method| XS Test CR | SCOPE CR | Orbench CR | Phtest CR | OKTest CR | Avg CR | Advbench SS | Tradeoff Score |
|-|-|-|-|-|-|-|-|--|
| ACTOR (**n=15**) | 94.67 | 89.88 | 72.76| 96.21 | 94.00| 89.50 | 98.85 | 94.17 |
| ACTOR (**n=50**) | 95.00| 90.39 | 73.09 | 96.21| 93.67| 89.60| 99.03| 94.31|
Similarly, we also conducted additional ablation experiments by selecting **10** and **50** random over-refusal queries from the abovementioned datasets-
| Method | XS Test CR | SCOPE CR | Orbench CR | Phtest CR | OKTest CR) | Avg CR| Advbench SS | Tradeoff Score |
|-|-|-|-|-|-|-|-|-|
| ACTOR (**n=10**)| 95.33 | 90.05| 73.01| 95.90 | 94.00| 89.65| 99.00 | 94.32 |
| ACTOR (**n=50**) | 95.33| 91.91| 74.98 | 96.81| 93.67| 90.54| 98.75| 94.65|
We also want to highlight that our method remains effective even under **low data budgets**. As shown in Fig 4, using **only 25 over‐refusal queries** during training yields performance gains that **surpass SFT trained on 100 over‐refusal queries**, underscoring the **data efficiency** of our approach.
## (D)
We agree that adding analysis on specific categories would make the paper more rich. XSTest, ORBench-Hard-1k and SCOPE are the benchmarks with such categories included. We show the Compliance Rates on these categories before and after intervention with ACTOR [here](https://limewire.com/d/HGAko#HqHk2E8Qst).
[1] Surgical, Cheap, and Flexible: Mitigating False Refusal in Language Models via Single Vector Ablation | Summary: Language Models (LMs) must balance refusing unsafe prompts while complying with benign ones. Despite safety training, LMs often refuse benign prompts that contain spurious correlations with harmful ones, a behavior known as over-refusal. This paper introduces ACTOR, a technique inspired by representation engineering. This technique involves first identifying a refusal direction in activation space and then fine-tuning a target layer to minimally shift model activations along this direction based on labels indicating the harmfulness of the training query. Empirical evidence shows that this representation-based technique is more data-efficient and task-performant than traditional Supervised Fine-Tuning (SFT).
Claims And Evidence: The paper provides strong empirical evidence for its claims. Beyond studying over-refusal directly, the paper benefits from comparing against test-time steering interventions which are, at present, a popular approach in the literature.
However, the paper focuses on single-turn harmful prompts. While this is a common evaluation setup in the literature, it is unclear whether the robustness generalizes to challenging multi-turn attacks [1, 2] which may represent a more realistic threat model [3]. I suggest that the authors either include multi-turn experiments or acknowledge this gap as a potential limitation in the generalization of their results.
[1] - Russinovich, M., Salem, A., & Eldan, R. (2024). Great, Now Write an Article About That: The Crescendo Multi-Turn LLM Jailbreak Attack. ArXiv, abs/2404.01833.
[2] - Li, N., Han, Z., Steneker, I., Primack, W.E., Goodside, R., Zhang, H., Wang, Z., Menghini, C., & Yue, S. (2024). LLM Defenses Are Not Robust to Multi-Turn Human Jailbreaks Yet. ArXiv, abs/2408.15221.
[3] - Haider, E., Perez-Becker, D., Portet, T., Madan, P., Garg, A., Majercak, D., Wen, W., Kim, D., Yang, Z., Zhang, J., Sharma, H., Bullwinkel, B., Pouliot, M., Minnich, A., Chawla, S., Herrera, S., Warreth, S., Engler, M., Lopez, G., Chikanov, N., Dheekonda, R.S., Jagdagdorj, B., Lutz, R., Lundeen, R., Westerhoff, T., Bryan, P., Seifert, C., Kumar, R.S., Berkley, A., & Kessler, A. (2024). Phi-3 Safety Post-Training: Aligning Language Models with a "Break-Fix" Cycle. ArXiv, abs/2407.13833.
Methods And Evaluation Criteria: The evaluation metrics and datasets fit the proposed research questions. The paper especially benefits from studying out-of-distribution (OOD) robustness, data efficiency, and multi-turn overall performance.
Theoretical Claims: The paper motivates the proposed technique with theoretical claims regarding the geometry of refusal. The paper cautions that the theoretical intuition serves as a useful motivation for the technique but does not serve as proof in its own right and is thus not to be considered a core contribution of the work. I did not attempt to prove these claims and instead rely on the empirical evidence as support for these theoretical claims.
Experimental Designs Or Analyses: I did check the experiment design and read the papers for the leveraged benchmarks. This experiment design is in line with the existing literature. The authors acknowledge that using a variety of refusal/safety benchmarks can have the confounding factor of variance in the labeling policies of the benchmark authors.
Supplementary Material: NA
Relation To Broader Scientific Literature: Over-refusal is a prominent challenge in modern LM safety training. This work makes a valuable contribution by showing that focusing on optimizing against internal representations during train-time can outperform traditional fine-tuning as well as dynamic test-time steering techniques.
Essential References Not Discussed: There are no obvious missing references that aren't considered concurrent work.
Other Strengths And Weaknesses: Strength: This work is well-written, especially the section describing the theoritical motivations of the technique.
Weakness: The paper seems to use a custom GPT-4o prompt for refusal and harm classification. There are existing classifiers int he literature for this task such as HarmBench [1], LlamaGuard [2], and Wild Guard [3]. Using a custom prompt makes comparisions across papers more difficult.
[1] - Mazeika, M., Phan, L., Yin, X., Zou, A., Wang, Z., Mu, N., Sakhaee, E., Li, N., Basart, S., Li, B., Forsyth, D., & Hendrycks, D. (2024). HarmBench: A Standardized Evaluation Framework for Automated Red Teaming and Robust Refusal. ArXiv, abs/2402.04249.
[2] - Inan, H., Upasani, K., Chi, J., Rungta, R., Iyer, K., Mao, Y., Tontchev, M., Hu, Q., Fuller, B., Testuggine, D., & Khabsa, M. (2023). Llama Guard: LLM-based Input-Output Safeguard for Human-AI Conversations. ArXiv, abs/2312.06674.
[3] - Han, S., Rao, K., Ettinger, A., Jiang, L., Lin, B.Y., Lambert, N., Choi, Y., & Dziri, N. (2024). WildGuard: Open One-Stop Moderation Tools for Safety Risks, Jailbreaks, and Refusals of LLMs. ArXiv, abs/2406.18495.
Other Comments Or Suggestions: There is a typo on line 330.
Questions For Authors: My understanding is that the authors perform full-parameter fine-tuning for the target layer. Have the authors looked into parameter-efficient techniques like LoRA? Successful parameter-efficient experiments can further demonstrate the effectiveness of the technique and allow experimentation with even larger models.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate your thoughtful remarks and the positive rating you assigned to our paper. Below, you'll find our responses, which we hope clarify the points you raised.
## (A)
While multi‐turn attacks indeed pose a more realistic challenge, there are currently no established benchmarks specifically designed for multi‐turn over‐refusal scenarios. Evaluating both multi‐turn over-refusal and multi‐turn safety, as well as understanding how they intersect, remains an open research problem. We therefore leave this exploration to future work, and we appreciate your suggestion to further examine the robustness of our method in more complex dialog settings.
## (B)
We found that existing classifiers such as HarmBench, LlamaGuard, and WildGuard can be overly conservative for the pseudo-harmful queries used in our benchmarks, often flagging them as harmful. For example- **LlamaGuard classifies 33% of the total queries from ORBench-Hard-1k as harmful**.
Earlier approaches [1][2] in our line of work include human evaluation and string matching for evaluation. To achieve a balance between context‐awareness, reproducibility, and scalability we opted for an LLM judge with a carefully crafted system prompt—an approach used extensively in related literature [3]. We provide all relevant prompts and details in Appendix E, allowing others to replicate our setup and compare results more directly.
## (C)
Since our current approach only fine-tunes a single layer—already providing a relatively efficient setup—we consider integrating LoRA into our design as an exciting avenue for further increasing parameter efficiency and performance even on larger models.
Thanks again for the valuable suggestions.
[1] Cao, Zouying, Yifei Yang, and Hai Zhao. "Nothing in excess: Mitigating the exaggerated safety for llms via safety-conscious activation steering." arXiv preprint arXiv:2408.11491 (2024).
[2] Wang, Xinpeng, et al. "Surgical, Cheap, and Flexible: Mitigating False Refusal in Language Models via Single Vector Ablation." arXiv preprint arXiv:2410.03415 (2024).
[3] Qi, Xiangyu, et al. "Fine-tuning aligned language models compromises safety, even when users do not intend to!." arXiv preprint arXiv:2310.03693 (2023).
---
Rebuttal Comment 1.1:
Comment: Thank you for responding to my questions. My score remains unchanged.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer b27H,
We are happy to hear that our responses have addressed your concerns and questions. We appreciate you taking the time to read our rebuttal and adjust your evaluation accordingly. We will incorporate all the clarifications, additional experimental results, and suggested modifications discussed during the rebuttal into our revised version. Thank you once again for your valuable, constructive feedback and for your consideration.
Best regards,
Authors | Summary: This paper focuses on addressing the over-refusal issue in aligned LLMs. The proposed technique, ACTOR, leverages internal activation for fine-tuning a single layer of the model to reduce the over-refusal rate.
## update after rebuttal
Thanks for the authors' response, which addresses most of my concerns.
Claims And Evidence: Overall, most evidence is clearly presented. However, I have some concerns regarding the limitations of existing work claimed in Section 2, which I did not find references or evidence to support, for example (not limited to)
> These
inference-time solutions, while computationally efficient,
are highly sensitive to initial data distributions, leading to
inconsistent performance across different contexts. Additionally, these approaches offer a one-size-fits-all solution
and typically do not provide differentiated treatment for various types of queries.
Methods And Evaluation Criteria: The proposed method, using representation vectors for fine-tuning, intuitively makes sense. However, it seems directly applying representation fine-tuning methods in this scenario, so I think the novelty can be further justified.
Theoretical Claims: The theoretical analysis is correct but overly simplified and straightforward. Moreover, it does not align with other main claims made in this paper, e.g. why ”Just Enough” Shift does not harm natural performance or why a single layer is sufficient to achieve the fine-tuning.
Experimental Designs Or Analyses: Mostly comprehensive, subject to the coverage of models, datasets, and ablation studies. However, the experiment only includes SFT and SCANS as baselines, missing comparison with other broad existing methods discussed in this paper. There is also a lack of an ablation study on the selection of the fine-tuning layer.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: Addressing the over-refusal problem could benefit the balance between safety and utility of LLMs.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Some figures/tables are overly large/small. A better format is appreciated.
Other Comments Or Suggestions: See above sections.
Questions For Authors: See above sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. Below, you'll find our detailed responses, which we hope clarify the points you raised.
## (A)
We appreciate the opportunity to clarify the basis of our claims in Sec 2. While we had experimental results (Sec 4) that support these points, we realize they were not explicitly cited. We will revise the manuscript to better link these findings to our claims.
1. We claim that SCANS and the “surgical” method [1]—are highly sensitive to the specific datasets used to derive their refusal vectors. In Figure 5, we show that SCANS exhibits significant performance fluctuations when we vary the harmful datasets used. Likewise [1] also exhibits similar variance when switching among different pseudo-harmful datasets.
| Method| OR Compliance Rate |
|-|-|
| Surgical (ORB-H) | 86.39|
| Surgical (OKTest) | 63.88 |
2. We also claimed that SCANS and [1] offer a uniform, one-size-fits-all adjustment to the model, applying the same refusal vector—regardless of each query’s unique activation patterns. This approach can lead to unnecessary or insufficient corrections, as each query requires a different level of ablation to ensure compliance (Sec 3.2).
**ACTOR’s Adaptive Mechanism**: In contrast, our proposed approach employs a **dynamic training objective**- moving ahead from specific task vectors. ACTOR repeatedly updates both the model parameters and the refusal direction during fine-tuning, enabling an **input-dependent shift** proportional to each query’s projection onto the refusal direction. This underpins ACTOR’s robustness; it is not limited to a single axis correction but leverages the full capacity of the model’s internal activation space to maintain robust performance even under distributional shifts (Fig 5). As shown by our experimental results in the paper (Tables 1–4) and the addition of new baselines (Reviewer eEU9 response (C))- ACTOR outperforms all baselines in balancing both compliance and safety. We have also included a table comparing existing methods with ACTOR to further support our claims on their limitations in our response to Reviewer eEU9 (C).
## (B)
We would like to clarify that ACTOR is distinct from ReFT in both design and motivation.
1. **Parametrization**: Rather than introducing **additional parameters**, ACTOR **fine-tunes a single layer** of the original model, avoiding the overhead associated with auxiliary interventions.
2. **Learning Objective**: Its objective departs from standard output-based losses by encouraging a **“just enough” shift** in the model’s internal representations, scaled by each query’s specific projection onto the refusal direction. This prevents both excessive and insufficient corrections, which can result when a one-size-fits-all approach is applied.
3. **Annotated Data**: Unlike ReFT, ACTOR does not rely on full response supervision as it draws on internal activation information as its supervision signal making it more **cost-effective** and straightforward to deploy.
Motivationally, ACTOR is designed for cases where the degree of over-refusal varies by query, requiring individualized corrections (Sec 3.2). This focus drives both the training algorithm and the learning objective, ensuring a reduction in over-refusal while being computationally light. We will revise the appropriate sections to highlight these distinctions and justify our novelty.
## (C)
We would like to clarify that the **intent of the theoretical analysis** is **not to explain** why the “Just Enough” Shift preserves natural performance or why fine-tuning a single layer is sufficient. Rather, as stated in Lines 231–233, the theory is designed to offer **intuition behind the design of our training objective**—specifically, why subtracting out the projected activation shift with the refusal direction enables targeted correction for over-refusal, without imposing a uniform change across all inputs.
We agree that theory is simplified to maintain clarity and provide a conceptual foundation for the method’s core ideas. It is **not intended to serve as a comprehensive performance guarantee.**
As for the claims regarding natural performance preservation and single-layer sufficiency, we **support these empirically** through extensive experiments in Sec 4.2.
1. The “Just Enough” Shift mechanism maintains high performance on benign queries (Table 1)
2. Fine-tuning a single layer already yields substantial improvement in over-refusal mitigation without degrading natural performance (Table 3).
We will revise the text to clarify the scope and role of the theoretical analysis and explicitly distinguish it from our empirical findings.
## (D)
**Comparison With Baselines**: Kindly refer to our rebuttal to Reviewer eEU9 (C)
**Ablation Study on the Fine-Tuning Layer**: An ablation on the choice of the fine-tuning layer is present in Appendix C.1
[1] Surgical, Cheap, and Flexible: Mitigating False Refusal in Language Models via Single Vector Ablation
---
Rebuttal Comment 1.1:
Comment: Thanks for the authors' response, which addresses most of my concerns. Though clarified by the authors, I still think the novelty and theoretical contributions are somewhat weak, but I appreciate the technical and empirical part of this work. Thus I have raised my score and am not opposed to acceptance.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer Fyfs,
We are happy to hear that our responses have addressed your concerns and questions. We appreciate you taking the time to read our rebuttal and adjust your evaluation accordingly. We will incorporate all the clarifications, additional experimental results, and suggested modifications discussed during the rebuttal into our revised version. Thank you once again for your valuable, constructive feedback and for your consideration.
Best regards,
Authors | null | null | null | null | null | null |
TSP: A Two-Sided Smoothed Primal-Dual Method for Nonconvex Bilevel Optimization | Accept (poster) | Summary: This paper investigates a bilevel optimization problem where both the upper and lower levels are nonconvex, making it a challenging problem. The author proposes a smoothed-type single-loop algorithm and provides a theoretical complexity guarantee for convergence to a KKT-type stationary point. Numerical experiments are conducted to demonstrate the performance of the proposed algorithm.
## update after rebuttal: I appreciate the authors’ response. I agree that the existing hardness results, while closely related, do not contradict the findings presented in the paper. If the results are indeed correct, this would be a strong and impactful contribution.
Claims And Evidence: Yes, it is clear.
Methods And Evaluation Criteria: Yes, the algorithm is tested on standard machine learning tasks.
Theoretical Claims: I find the key contribution of this paper to be its ability to handle nonconvexity in the lower-level problem, which, to my knowledge, has been a significant challenge in bilevel optimization. As claimed by the authors, the proposed algorithm reaches a stationary point satisfying the KKT conditions for both the upper and lower levels under only a weakly convex assumption. This result appears quite strong. Given that lower bound results exist for related problems (such as in minimax optimization, which is a special case considered in this paper), [1] shows that such problems are PPAD-hard (though with additional constraints). Could the authors provide insights into why their approach successfully achieves this result despite these known hardness barriers? Understanding this aspect would further clarify the theoretical significance of the proposed method.
[1] Daskalakis, Constantinos, Stratis Skoulakis, and Manolis Zampetakis. "The complexity of constrained min-max optimization." Proceedings of the 53rd Annual ACM SIGACT Symposium on Theory of Computing. 2021.
Experimental Designs Or Analyses: The experimental design makes sense to me. However, it would be helpful if the authors could explain how the chosen parameters in the experiments align with the theoretical claims. Providing this clarification would strengthen the connection between the theoretical guarantees and empirical results.
Supplementary Material: I have reviewed the supplementary material but have not conducted a detailed verification of its correctness.
Relation To Broader Scientific Literature: This work makes significant progress in bilevel optimization by removing the convexity assumption, which is a notable advancement in the literature.
Essential References Not Discussed: Not found.
Other Strengths And Weaknesses: If the results are correct, the problem studied in this paper could be highly significant.
Other Comments Or Suggestions: - line 195: formulations (1) and (1)
- line 215: forgotten period at the end.
- line 255 & 256: should the UL and LL get exchanged?
Questions For Authors: Please review the theoretical sections. I will definitely increase my score if I can confirm the correctness of the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank reviewer fDFn for your helpful comments and questions.
**Theoretical Claims:**
*I find the key contribution of this paper to be its ability to handle nonconvexity in the lower-level problem, which, to my knowledge, has been a significant challenge in bilevel optimization. As claimed by the authors, the proposed algorithm reaches a stationary point satisfying the KKT conditions for both the upper and lower levels under only a weakly convex assumption. This result appears quite strong. Given that lower bound results exist for related problems (such as in minimax optimization, which is a special case considered in this paper), [1] shows that such problems are PPAD-hard (though with additional constraints). Could the authors provide insights into why their approach successfully achieves this result despite these known hardness barriers? Understanding this aspect would further clarify the theoretical significance of the proposed method.*
> Thank you for your insightful comment. The main source of hardness in solving min-max problems (a special case of bilevel optimization) to the type of stationary points defined in [1] lies in the presence of constraints. In our setting, there are **no explicit constraints** at either the upper or lower level.
> Additionally, we assume that the objective functions are **coercive**, which helps ensure that the iterates generated by our SPD algorithm remain within a bounded region without requiring additional projection. As a result, this assumption—together with the algorithm design—implicitly guarantees the boundedness of the loss values over the unconstrained domain.
> These conditions align exactly with the discussion following Theorem 4.1 in [1], which argues that in such unconstrained settings with bounded loss value, approximate stationary points **do** exist and can be found in **polynomial time**. Therefore, our theoretical results do not contradict known hardness barriers; rather, they fall within a subclass of problems where efficient solutions remain tractable.
*[1] Daskalakis, Constantinos, Stratis Skoulakis, and Manolis Zampetakis. "The complexity of constrained min-max optimization." Proceedings of the 53rd Annual ACM SIGACT Symposium on Theory of Computing. 2021.*
**Experimental Designs Or Analyses:**
*The experimental design makes sense to me. However, it would be helpful if the authors could explain how the chosen parameters in the experiments align with the theoretical claims. Providing this clarification would strengthen the connection between the theoretical guarantees and empirical results.*
>Thank you for the helpful comment. The parameter choices (primarily the learning rates) were selected via grid search, following standard practice in the literature. For the stochastic case, we applied a learning rate decay of $ 1/\sqrt{r}$, which is guided by our theoretical results. The initial learning rates were determined through grid search.
> We also apologize for the typo in line 418 of the paper: the learning rate decay was incorrectly written as $1/r$; it should be $1/\sqrt{r}$. We will correct this in the revised version.
**Other Comments Or Suggestions:**
*line 195: formulations (1) and (1)*
> Typo: the second reference to equation (1) should be (3).
>
*line 215: forgotten period at the end.*
> Thank you for your careful reading. We will add the missing period in the revised version.
*line 255 & 256: should the UL and LL get exchanged?*
> The terms "UL'' and "LL'' are indeed confusing in this context. We will remove them in the revised version. | Summary: This paper proposed a single-loop method for solving the stochastic bilevel optimization problem with weakly convex lower-level problem. The proposed method is proved to achieve a convergence rate of $O(\epsilon^{-4})$ in terms of a smoothed reformulation. Some experimental results on data hyper-cleaning task and representation learning task are presented to show that the proposed method outperfumes some existing methods.
Claims And Evidence: This paper claims that the proposed method better solves the stochastic bilevel optimization problem in terms of both convergence rate and experimental performance. For the theoretical analysis part, my main concern is the gap between the penalty reformulation and the original bilevel problem. It seems that both of the proposed method and the convergence analysis are based on the reformulation. It is unclear that how the convergence guarantee relates to the original problems.
Methods And Evaluation Criteria: The main idea of the method design is to reformulate the original bilevel optimization problem into a min-max optimization problem with more feasible conditions using moreau envelope and penalty technique. This makes sense as the reformulated problem is a convex-linear min-max problem is well-studied and easier to solve.
Theoretical Claims: Please see the Claims And Evidence section.
Experimental Designs Or Analyses: Regarding the baselines in the experiments, I have the following concerns/questions.
1. Regarding the data hyper-cleaning task, as described in section 4, the lower-level objective is the cross-entropy loss function, which is convex. This problem can be solved by methods designed for bilevel problems with convex lower-level problems. This application seems not suitable. The authors need to either compare SPD with the convex LL methods or choose a 'merely' weakly convex LL problem as the application.
2. All the baselines compared in the experiments are in deterministic setting, which makes the experimental results not very convincing. Moreover, it is well known that stochastic methods generalize better than deterministic methods in general. Thus, the claim 'This example further highlights the advantage of solving bilevel learning problem through the lens of equilibrium constrained optimization' in the representation learning task part may not necessarily hold.
Supplementary Material: I partially reviewed the supplementary material, including the statements of the main results.
Relation To Broader Scientific Literature: The main contribution of this work is that it is trying to weaken the convexity assumption on the lower-level objective of bilevel optimization, which is essential as it covers a larger family of problems.
Essential References Not Discussed: All essential references that I'm aware of are discussed.
Other Strengths And Weaknesses: I do not see other strengths and weaknesses.
Other Comments Or Suggestions: 1. In Assumption 3.1, the weak-convexity assumption A2 is unnecessary as it is implied by the smoothness assumption A1.
2. Using $G(x,y;\xi_i)$ for single sample stochastic estimator, and $\hat{g}(x,y)$ for mini batch stochastic estimator is rather confusing. It would help the readers to understand more easily if such notations are more consistent.
Questions For Authors: I do not have any other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank reviewer bXuu for your helpful comments and questions.
**Claims And Evidence:**
*My main concern is the gap between the penalty reformulation and the original bilevel problem. It seems that both of the proposed method and the convergence analysis are based on the reformulation. *
> Correct. The proposed method addresses a Moreau envelope-based reformulation of the original bilevel optimization problem. The relationship and equivalence between the original and reformulated problems are discussed between lines 194 and 199 of the paper, summarizing the findings of existing works [Gao et al., 2023] and [Liu et al., 2024a].
>
> The equivalence presented in [Theorem A.2, Liu et al., 2024a] for the simplified case where the lower-level problem is unconstrained is further clarified below.
>
> **Original Problem:**
> $$
> \min_{x, y} f(x, y), \quad \text{s.t.} \quad y \in \mathcal{S}(x)
> $$
> where $\mathcal{S}(x) := \arg\min_y g(x, y)$.
>
> **Moreau Envelope-based Reformulation:**
> $$
> \min_{x, y} f(x, y), \quad \text{s.t.} \quad g(x, y) - g^\star_\gamma(x) \le 0
> $$
>
> - When the lower-level function $g(x, y)$ is convex or satisfies the Polyak-Łojasiewicz (PL) condition, these two formulations are equivalent.
> - When $g(x, y)$ is weakly convex and $\gamma \in (1, 1/\rho)$, the Moreau envelope-based reformulation becomes equivalent to a relaxed version of the original problem:
> $$
> \min_{x, y} f(x, y), \quad \text{s.t.} \quad y \in \mathcal{S}'(x)
> $$
> where $\mathcal{S}'(x) := \\{ y \mid \\|\nabla_y g(x, y)\\| = 0 \\}$
> Given the weak convexity of $g$, it is reasonable to aim for a stationary point, as opposed to requiring a global optimum for the lower-level problem.
**Methods And Evaluation Criteria:**
The main idea of the method design is to reformulate the original bilevel optimization problem into a min-max optimization problem with more feasible conditions using moreau envelope and penalty technique. This makes sense as the reformulated problem is a convex-linear min-max problem is well-studied and easier to solve.
> Yes, this approach is conceptually related to the primal-dual or Lagrangian methods. However, the reformulated problem is **not** a convex-linear min-max problem due to the weak convexity of both the upper- and lower-level objective functions. Therefore, standard techniques for solving convex-linear min-max problems are not directly applicable in this case.
> The main reasons are as follows:
> 1. The upper-level objective function $f(x, y)$ are nonconvex rather than convex.
> 2. The lower-level function $g(x, y)$, even after applying the Moreau envelope, does not necessarily yield a convex constraint.
**Experimental Designs Or Analyses:**
*Regarding the data hyper-cleaning task, as described in section 4, the lower-level objective is the cross-entropy loss function, which is convex. This problem can be solved by methods designed for bilevel problems with convex lower-level problems. This application seems not suitable. *
> As noted on line 382, the lower-level objective includes a nonconvex regularization term. While the cross-entropy loss $\ell_{\text{tr}}$ is convex, the presence of the nonconvex regularizer makes the overall lower-level function **weakly convex**. Therefore, this data hyper-cleaning task remains a suitable example for evaluating methods designed for bilevel problems with weakly convex lower-level objectives.
*All the baselines compared in the experiments are in deterministic setting, which makes the experimental results not very convincing. Moreover, it is well known that stochastic methods generalize better than deterministic methods in general. Thus, the claim 'This example further highlights ... optimization' in the representation learning task part may not necessarily hold.*
> Please kindly note that the numerical experiments on the representation learning task are conducted in a **stochastic setting**. As mentioned on line 418, a batch size of 32 is used. This setting is applied to all compared algorithms, indicating that they are all implemented stochastically. We will clarify this more explicitly in the revised version to ensure it is clear that **all methods are evaluated in a stochastic manner** for a fair comparison.
**Other Comments Or Suggestions:**
*In Assumption 3.1, the weak-convexity assumption A2 is unnecessary as it is implied by the smoothness assumption A1.*
> Thank you for your comment. We will remove Assumption A2 in the revised version.
*Using $G(x,y;\xi_i)$ for single sample stochastic estimator, and $\hat{g}(x,y)$ for mini batch stochastic estimator is rather confusing. It would help the readers to understand more easily if such notations are more consistent.*
> Thank you for the helpful suggestion. We will use $\nabla \hat{G}(x, y)$ to denote the mini-batch stochastic gradient estimator, so that the notation is more consistent throughout the paper.
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed rebuttal. My concern on the gap between the penalty reformulation and the original bilevel problem is resolved. Their connections seem to be well-studied in existing works as the authors explained. The baselines in the experiments make sense now as they are implemented in stochastic manner, which makes a fair comparison.
Regarding my other concerns:
>Yes, this approach is conceptually related to the primal-dual or Lagrangian methods. However, the reformulated problem is not a convex-linear min-max problem due to the weak convexity of both the upper- and lower-level objective functions.
You are right. I meant to say that the reformulated problem is a weakly-convex-linear min-max problem. But still, it is a well-studied problem, which makes the contribution of the analysis less strong.
>As noted on line 382, the lower-level objective includes a nonconvex regularization term. While the cross-entropy loss
is convex, the presence of the nonconvex regularizer makes the overall lower-level function weakly convex.
This is still confusing to me. The lower-level problem in the data hyper-cleaning task is $\ell_{tr}(x,y')+\bar{\rho} \ \text{reg}(x)$, which is essentially just the cross-entropy loss in terms of $y'$, thus is convex in $y'$. The 'nonconvex regularization term' is independent from $y'$. What is the intuition of adding this regularization term? Is this a standard technique in data hyper-cleaning task?
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer bXuu,
We’re glad to hear that our response addressed your concerns regarding the gap between the penalty reformulation and the original bilevel problem, as well as the setup of our numerical experiments.
We also appreciate your follow-up questions. Our detailed responses are provided below.
> I meant to say that the reformulated problem is a weakly-convex-linear min-max problem. But still, it is a well-studied problem, which makes the contribution of the analysis less strong.
**Response**
- (**Inequivalence between min-max problem and primal-dual problem**)
The key difference between a min-max problem and a primal-dual formulation lies in the boundedness of the Lagrange multiplier (i.e., the maximizer).
Please note that the reformulated problem takes the form (see Equations (4) to (6) for details):
$$
\min_{x,y} \max_{\lambda \ge 0} f(x,y) + \lambda \big(g(x,y) - g^{\star}_{\gamma}(x,y) - \delta\big)
$$
where the feasible set of the dual variable (maximizer) is **unbounded**.
- (**Insufficiency of using general min-max solvers**)
While the problem is indeed weakly-convex-linear in min-max form, it involves an **unbounded** dual variable $\lambda$. Existing solvers for weakly-convex-linear min-max problems typically assume that the maximizer lies in a **compact** set (this assumption that does *not* hold in our case).
- (**Pitfalls of applying general min-max solvers blindly**)
The reformulated min-max structure arises from a constrained optimization setting. The existence of KKT points depends on the structure of the constraint term
$g(x,y) - g^{\star}_{\gamma}(x,y) - \delta$.
If one were to apply a generic min-max solver without accounting for this structure, it would imply that any weakly-convex constrained optimization problem (where both objective and constraints are weakly convex) could be solved without additional regularity conditions — an implication that is clearly *incorrect*.
- (**Significance of our method**)
Our work specifically addresses this class of min-max problems and establishes convergence of the iterates generated by SPD to approximate KKT points, satisfying stationarity, feasibility, and complementary slackness. We also prove that the dual variable (i.e., the maximizer $\lambda$) remains **bounded** under the SPD framework, which holds for the class of bilevel optimization-oriented constraints we consider.
> The lower-level problem in the data hyper-cleaning task is
$\ell_{tr}(x,y')+\bar{\rho}\textrm{reg}(x)$, which is essentially just the cross-entropy loss in terms of $y'$, thus is convex in $y'$. The 'nonconvex regularization term' is independent from $y'$. What is the intuition of adding this regularization term? Is this a standard technique in data hyper-cleaning task?
**Response:**
- Apologies for the typo.
- The regularization term should be
$$
\sum_{i=1}^d \frac{y'^2_i}{1 + y'^2_i}
$$
where $d$ is the dimensionality of the lower-level variable $y'$.
- (**Intuition of Adding This Term**) This type of nonconvex regularization encourages sparsity, similar to $\ell_1$ regularization, but with a key difference: it doesn’t overly penalize large coefficients.
- For small values of $y'_i$,
$\frac{y'^2_i}{1 + y'^2_i} \approx y'^2_i$ — like $\ell_2$ regularization.
- For large values of $y'_i$,
$\frac{y'^2_i}{1 + y'^2_i} \approx 1$ — so the penalty saturates.
This makes it a balanced choice for inducing sparsity while retaining significant features.
- (**Standard Technique**) This class of penalty functions is commonly used in sparse modeling, feature selection, and robust learning—especially in neural networks. In the context of data hyper-cleaning, the lower-level variables correspond to neural network weights. Using this kind of regularization helps improve robustness by selectively suppressing unreliable or noisy components without removing important ones entirely.
We sincerely thank the reviewer for these insightful questions. We will incorporate this discussion into the revised version to make the statements clearer and the contributions stronger. | Summary: This paper presents a smoothed primal-dual algorithm for solving stochastic bilevel optimization problems where the lower level problem is possibly nonconvex.
The authors first use Moreau envelope reformulation for the lower level problem and then use the smoothed primal-dual method to solve the resulting constrained optimization problem.
They establish the optimal convergence rate of the algorithm.
Claims And Evidence: Yes, no major issue.
Methods And Evaluation Criteria: Yes
Theoretical Claims: I checked the proof sketch and did not find major issues.
Experimental Designs Or Analyses: I briefly checked them and did not find any major issues.
Supplementary Material: Briefly checked the proof sketch.
Relation To Broader Scientific Literature: Nonconvex bilevel optimization is important in machine learning, AI, engineering and economics.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strength:
1.The algorithm can solve bilevel optimization with nonconvex lower level problem and achieve the optimal rate for stochastic problem with mild assumptions.
2. For the convergence analysis of primal-dual algorithm, they prove the boundedness of the dual variable instead of making bounded dual assumption.
Weakness:
See the questions below.
Other Comments Or Suggestions: See questions below.
Questions For Authors: Questions:
1. Is $p$ changing for different $r$? Could the authors specify the value of $p$ we should take in the algorithm and main theorem?
2. How does the algorithm in this paper compare to ``SLM: A smoothed Lagrangian method for structured nonconvex constrained optimization''? Could the authors provide details?
3. The Moreau envelope reformulation is proposed in previous papers. Could the authors provide more details about the novelty compared to these papers?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer 85Pr for your positive feedback, thoughtful comments, and constructive questions.
Questions:
*Is $p$ changing for different? Could the authors specify the value of $p$ we should take in the algorithm and main theorem?*
> In theory, $p$ is a constant and should be chosen to be on the same order as the dual variable, which is upper bounded by a constant. In practice, we can initialize it as a small value and increase it if the algorithm does not sufficiently decrease the loss, following a similar philosophy to tuning the learning rate.
*How does the algorithm in this paper compare to ``SLM: A smoothed Lagrangian method for structured nonconvex constrained optimization''? Could the authors provide details?*
> In comparison to the referenced work, the main differences are as follows:
> - (**Different class of lower-level problems**) The algorithms are designed for different bilevel optimization formulations. Our work focuses on a Moreau envelope-based reformulation, where the lower-level problem is weakly convex. In contrast, the referenced work assumes that the lower-level objective satisfies the PL condition.
> - (**Stochastic vs. deterministic setting**) Our algorithm is designed for the stochastic setting, whereas the referenced method addresses only the deterministic case. This distinction introduces significant challenges, particularly in designing the update rule for the dual variable under stochastic noise.
> - (**Single-loop vs. double-loop structure**) Our algorithm adopts a single-loop structure, which is more suitable for stochastic optimization. The referenced method, on the other hand, uses a double-loop approach.
> - (**New high-probability error bounds**): Our theoretical analysis explicitly quantifies stochastic errors arising from the updates of the upper-level variable, lower-level variable, and auxiliary variables. This includes handling the non-negativity constraint on the dual variable. As a result, the analysis framework is significantly different from that of the referenced work.
*The Moreau envelope reformulation is proposed in previous papers. Could the authors provide more details about the novelty compared to these papers?*
> The main novelties of this work, compared to previous papers that also study the Moreau envelope reformulation, are as follows:
> -(**Primal-Dual Update Strategy**): To the best of our knowledge, this is the first work that applies a primal-dual algorithm to solve the Moreau envelope-based bilevel optimization problem. It is well-established in the optimization community that primal-dual methods often achieve better convergence properties than penalty-based methods. This is largely due to the dynamic update of the dual variable, whereas penalty methods require either a sufficiently large penalty parameter or a monotonically increasing schedule, which can force the learning rate to be very small. This would be particularly problematic when handling multiple lower-level problems.
> -(**Stochastic Problem Formulation and Algorithm Design**) The proposed SPD method tackles a stochastic version of the Moreau envelope reformulation, which significantly broadens its applicability to real-world machine learning problems. In contrast, prior works have largely focused on deterministic settings. The stochastic nature of our formulation introduces substantial challenges in both algorithm design and theoretical analysis, particularly in achieving convergence guarantees. This further differentiates our approach from existing literature. | Summary: This paper introduces SPD (Smoothed Primal-Dual), a first-order gradient-based primal-dual method for solving bilevel optimization problems, potentially with a nonconvex lower-level problem. SPD is based on a Moreau envelope-based reformulation of the bilevel problem and employs a proximal primal-dual Lagrangian updating framework, eliminating the need for Hessian computations. Theoretical results on iteration complexity are provided, and numerical experiments are conducted to demonstrate the efficiency of the proposed method.
Claims And Evidence: This paper contains several inappropriate and incorrect claims:
At the beginning of the introduction, the authors state, "The mathematical programs with equilibrium constraints (Luo et al., 1996), also known as the bilevel optimization problem." This statement is incorrect, as mathematical programs with equilibrium constraints and bilevel optimization problems are distinct classes of problems.
On lines 69-71, the authors claim, "This property is advantageous from an optimization perspective, as the Slater condition holds automatically." This is incorrect because the Slater condition applies only to convex optimization problems, whereas (2) is clearly a nonconvex optimization problem.
In the contributions section (lines 167-169), the authors state that "this is the first time a stochastic first-order method has successfully achieved the KKT points of the bilevel optimization problem." However, in this work, they only demonstrate that their proposed method achieves an approximate KKT point, making this claim misleading.
Additionally, the reformulation (3) is incorrect.
Methods And Evaluation Criteria: The derivation of the proposed SPD algorithm in Section 2 lacks clarity. The authors claim that it is based on stochastic gradient-based updates to find the equilibrium points of $$\min_{x,y,\hat{x},\hat{y}}\max_{\lambda\geq 0}K(x,y,\hat{x},\hat{y},\lambda).$$ However, by the definition of $K(x,y,\hat{x},\hat{y},\lambda),$ the equilibrium points of this formulation must satisfy $\hat{x}=x, \hat{y}=y$. This raises concerns about the necessity of introducing the additional variables $\hat{x},\hat{y}$, as their inclusion may not contribute meaningfully to the optimization process. A clearer explanation should be provided to justify their role and the necessity of their updates.
Theoretical Claims: I have checked parts of the proof, and they appear to be sound.
Experimental Designs Or Analyses: The representation learning task in this paper lacks a clear problem setting and sufficient discussion. While the authors mention the use of a multi-head neural network structure, where the upper-level problem optimizes a shared model parameter layer and the lower-level problem consists of multiple task-specific heads, the details of how the bilevel structure is formulated and applied remain vague. The dataset split and the specific role of SPD in optimizing meta-learning objectives are not thoroughly explained. Furthermore, the experimental discussion is limited, with only a comparison of test accuracy and generalization performance across different methods.
Supplementary Material: No supplementary material has been provided.
Relation To Broader Scientific Literature: The proposed SPD is designed based on a Moreau envelope-based reformulation of the bilevel optimization problem (Gao et al., 2023; Yao
et al., 2024b; Liu et al., 2024a) and a moving average technique (Chen et al., 2023b).
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strength:
the experimental results demonstrate the practical advantages of the proposed method, showing improvements in test accuracy and generalization performance over other methods
Weaknesses:
1. The notation is quite confusing. For example, the variable **h** in the dual update is not properly explained, and the same symbol is used in the primal update to represent a different concept, which can cause confusion and make it difficult to follow the derivations.
2. There are an excessive number of equations, with a total of 244 equation labels. This creates a cluttered presentation and detracts from the clarity of the paper. It would be helpful to streamline the number of equations and provide better organization or referencing to make the paper more readable.
Other Comments Or Suggestions: In line 193, on the right hand side, "$\lambda^r+,\text{Proj}\geq 0$" should be $\lambda^r_{+},\text{Proj}_{\geq 0}$; in line 291, “beta” should be "$\beta$"; in line 685, "w.r.t. $x,y$” should be "w.r.t. $y$".
Questions For Authors: no
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank reviewer Dp7u for your helpful comments and questions.
**Claims And Evidence:**
*This statement about equilibrium constraints and bilevel optimization*
> Will remove that statement.
*On lines 69-71*
> Will remove the statement.
*contributions section (lines 167-169)*
> Will add "approximate''.
*Additionally, the reformulation (3) is incorrect.*
> The reformulation (3) should be:
$$
\min_{x,y} f(x,y):=\mathbb{E}_{\xi\sim D\_{UL}} F(x,y;\xi)
\\\\
\\quad \textrm{s.t.} g(x,y)- g^{\\star}\_{\gamma} (x,y)\le 0, \quad g^{\\star}\_{\gamma} (x,y):=\min_z \mathbb{E}\_{\xi\sim D\_{LL}} G(x,z;\xi)+\frac{1}{2\gamma}\\|z-y\\|^2.
$$
**Methods And Evaluation Criteria:**
Response:
> - Once the two quadratic proximal terms, $\frac{p}{2}\\|x - \hat{x}\\|^2$ and $\frac{p}{2}\\|y - \hat{y}\\|^2$, are introduced with auxiliary variables $\hat{x}$ and $\hat{y}$, the function $K(x, y, \hat{x}, \hat{y}, \lambda)$ becomes strongly convex. This strong convexity ensures the existence of a unique optimal solution for $x$, $y$, and $\lambda$, given any fixed $\hat{x}$ and $\hat{y}$. These optimal solutions are denoted as $x^{\star}(\hat{x}, \hat{y}; \lambda)$ or $\bar{x}^{\star}(\hat{x}, \hat{y})$, and similarly for $y$ (see equations (14) and (15) for details).
> - Based on this setup, we can quantify the convergence process of the iterates $(x^r, y^r, \lambda^r)$ by measuring the distance between $x^r$ and $x^{\star}(\hat{x}^r, \hat{y}^r; \lambda^{r+1})$, and similarly between $y^r$ and $y^{\star}(\hat{x}^r, \hat{y}^r; \lambda^{r+1})$. These distances can be further upper bounded by the successive differences of the iterates, i.e., $\\|x^{r+1} - x^r\\|^2$ and $\\|y^{r+1} - y^r\\|^2$, using the standard primal error bound (Zhang & Luo, 2020).
> - Therefore, the proximal terms are critical. In particular, the distances to the proximal mappings automatically shrink to zero, ensuring that the algorithm converges to the solution of the optimization problem. As such, the auxiliary variables $\hat{x}$ and $\hat{y}$ play a key role in the algorithm design and in quantifying its convergence to the KKT points of the original problem.
**Experimental Designs Or Analyses:**
*The representation learning task in this paper lacks a clear problem ... the details of how the bilevel structure is formulated and applied remain vague. *
> The representation learning task can be **formulated as a bilevel optimization problem**, as shown below:
$$
\min_{x,\{y_i\}} \quad f(x, \{y_i\}) := \mathbb{E}\_{\xi \sim \mathcal{D}^{\text{val}}} \left[\frac{1}{K} \sum_{i=1}^K \ell(x, y_i; \xi)\right]
\\\\
\text{s.t.} \quad y_i \in \arg\min_{y'_i} \mathbb{E}\_{\xi_i \sim D^{\text{tr}}_i} \ell(x, y'_i; \xi_i), \quad \text{for } i \in [K].
$$
> - $x$ represents the **shared model parameters**, typically corresponding to the **common feature encoder** or backbone network shared across all tasks.
> - $y_i$ denotes the **task-specific head parameters**, i.e., the final classification layer for task $i$, which is optimized using the task-specific training data $\mathcal{D}^{\text{tr}}_i$.
> - This formulation captures the core idea of our approach: learning a shared feature representation ($x$) that enables effective adaptation to multiple downstream tasks through task-specific parameters ($y\_i$).
*The dataset split and the specific role of SPD in optimizing meta-learning objectives are not thoroughly explained.*
> We use a custom split of the MNIST dataset, where we create eight sub-datasets, each corresponding to a single digit class. Each sub-dataset contains 2,500 training samples and 1,500 validation samples.
> - We use five sub-datasets for pretraining the model.
> - The remaining three sub-datasets are used for meta-learning, which includes both meta-training and meta-testing.
> The key role of SPD in this framework is to adjust the dual variables individually for each task-specific head. This flexibility helps to balance the optimization dynamics between the shared and task-specific components, which in turn improves the generalization capability of the learned representation across unseen tasks.
*Furthermore, the experimental discussion is limited.*
> For bilevel optimization problems, our experimental discussion is centered on evaluating the performance of the algorithms at both the upper and lower levels. We also include addtional results w.r.t training accuracy, convergence behavior, and runtime efficiency in the appendix, showing that the proposed SPD algorithm consistently achieves superior performance across these metrics.
**Weakness 1**
> - In the dual update, $h$ is an iterative variable that serves as a stochastic estimate of the gradient of the function $K(x, y, \hat{x}, \hat{y}; \lambda)$ .
> - While the symbol $h$ also appears in the primal update, each instance is clearly distinguished by different superscripts (e.g., $f$ or $g$) and subscripts.
**Weakness 2**
> Will remove unnecessary numbers. | null | null | null | null | null | null |
SADA: Stability-guided Adaptive Diffusion Acceleration | Accept (poster) | Summary: This paper proposes SADA, a novel paradigm that unifies step-wise and tokenwise sparsity decisions using a shared criterion based on the denoised latent x0. By aligning with modern numerical solvers that rely heavily on x0, SADA offers more stable pruning decisions and preserves important visual details throughout the denoising trajectory. Extensive experiments on SD 2 and SDXL demonstrate that SADA significantly accelerates inference without compromising image quality.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: This paper proposed a new cache-based accelerating method in the diffusion model area.
Essential References Not Discussed: No
Other Strengths And Weaknesses: **Strengths:**
1. The paper is well-organized and includes comprehensive technical details.
2. The authors provide sufficient theoretical analysis for the proposed method, including the proof of error bound.
3. The images generated by the proposed method are consistent with those produced by the original diffusion models.
**Weakness:**
1. This paper only presents experimental results on U-Net-based diffusion models. Since the state-of-the-art image diffusion models now primarily use DiT or MM-DiT architectures, it is essential to demonstrate the effectiveness of SADA on models like PixArt, Flux, or SD 3.
2. The evaluation setting for DPM-Solver++ uses 50 sampling steps. However, the main advantage of DPM-Solver is its ability to achieve high-generation quality with fewer sampling steps. Therefore, it would be more reasonable to set the sampling step of DPM-Solver++ to 20.
3. The proposed SADA performs worse than AdaptiveDiffusion when evaluated with DPM-Solver++. However, DPM-Solver++ holds greater practical value compared to the Euler solver.
4. As shown in the results, the acceleration ratio of SADA is around 1.5×. Can its speedup ratio be extended to 2× or beyond at the cost of some performance?
Other Comments Or Suggestions: N/A
Questions For Authors: Please see the weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the insightful and constructive comments.
**Q1: Can its speedup be extended to $2 \times$ or beyond?**
**A1:** Yes, it can. To apply an faster configuration, we leverage the inherent stability of the per‐step data reconstruction $x_0^t$. When the $x_0^t$ trajectory demonstrates high stability (e.g., the second half of Fig.2), we could employ larger step sizes compensated by higher-order approximations. Building on this insight, we implement a uniform step-wise pruning strategy after the stability of the denoising process with Lagrange interpolation for correction.
For example, consider a 50‐step process. To achieve a step-wise pruning interval of 4 after stable (i.e., compute every 4th step fully and interpolate the skipped steps via Lagrange), we store $\hat{x}_0^t$ every 4 steps before stabilization. Their indices define the fixed-size set $I$, which is updated dynamically to limit memory usage. For any skipped $t$:
$$
\hat{x}_0^{t}\gets\sum _{i \in I}\prod _{j\in I\setminus \\{ i \\}}\frac{t-t_j}{t_i-t_j}\hat{x}_0^{t_i}
$$
Under this setting, we yield a $\geq 1.8 \times$ speedup regardless of models or solvers. The acceleration would be even more aggressive if further increasing the step size.
To balance the degradation, we raise the Adams-Moulton approximation from second to third order, allowing $x_0^t$ to leverage information from the previous three steps (instead of two), thereby improving numerical accuracy and robustness. Our updated result in Table 1 demonstrates the effectiveness of the above improvements. Notably, we achieve a $2.02 \times$ speedup on the most powerful Flux.1 model with impressive $0.06$ LPIPS and $1.95$ FID.
**Table 1: Quantitative results on MS-COCO 2017**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**|**FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
|SD2|DPM++|DeepCache|17.70|0.271|7.83|1.43|
|||AdaptiveDiffusion|24.30|0.100|4.35|1.45|
|||SADA|**26.34**|**0.094**|**4.02**|**1.80**|
|SD2|Euler|DeepCache|18.90|0.239|7.40|1.45|
|||AdaptiveDiffusion|21.90|0.173| 7.58| **1.89**|
|||SADA | **26.25**|**0.100**|**4.26**|1.81|
|SDXL|DPM++| DeepCache|21.30|0.255|8.48|1.74|
|||AdaptiveDiffusion| 26.10|0.125|4.59|1.65|
|||SADA| **29.36**| **0.084**|**3.51**|**1.86**|
|SDXL|Euler|DeepCache|22.00|0.223|7.36|**2.16**|
|||AdaptiveDiffusion|24.33|0.168|6.11|2.01|
|||SADA|**28.97**|**0.093**|**3.76**|1.85|
|Flux|Flow-matching|TeaCache|19.14|0.216|4.89|2.00|
|||SADA|**29.44**|**0.060**|**1.95**|**2.02**|
**Q2: Ablations on DPM-Solver++**
We appreciate the reviewers for highlighting the practical importance of DPM++ and its ability to achieve high quality with fewer steps.
**a. SADA performs worse than AdaptiveDiffusion?**
To counterbalance the aggressive configuration, we increased the order of the Adams-Moulton approximation from second to third order. This enhancement incorporates additional information from the previous denoising trajectory, which in turn improves both accuracy and stability. As shown in Table 1, SADA now significantly outperforms AdaptiveDiffusion when used with DPM++.
**b. Set the sampling step to 20?**
Table 2 presents a comprehensive ablation study across various sampling steps. Our method achieves a 1.5× acceleration in the 25-step scenario with negletable difference. Furthermore, we observe that as the number of inference steps increases, the images generated by DPM++ initially change dramatically before converging when the base step is set to 25. An illustration, along with additional generation examples and comparisons, is available at the following link:
https://drive.google.com/file/d/168ovZu9fxcfY5PfE8F5AgkN4la6dvH9f/view?usp=sharing
**Table 2: Ablation studyon sampling steps**
|**Model**|**Scheduler**|**Steps**|**PSNR**|**LPIPS**|**FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
|SD-2|DPM++|50|26.34|0.094|4.02|1.80|
|||25|28.15|0.073|3.13|1.48|
|||15|29.84|0.072|3.05|1.24|
||Euler|50|26.25|0.100|4.26|1.81|
||| 25| 26.83| 0.088|3.87|1.48|
|||15|29.34|0.076|3.70|1.25|
|SDXL|DPM++|50|29.36|0.084|3.51|1.86|
|||25|30.84|0.073|2.80|1.52|
|||15|31.91|0.073|2.54|1.29|
||Euler|50|28.97|0.093|3.76|1.85|
|||25|29.42|0.085|3.13|1.50|
|||15|31.28|0.084|3.26|1.26|
**Q3. SADA for Flow-matching & DiT Architecture**
Under the flow matching objective, the model directly predicts the transportation vector field $dx/dt$ between noise and data distributions. Since the denoising trajectory is ODE-based, our criterion effectively measures its stability. Table 3 on Flux (DiT) shows that our method significantly outperforms the most recent work suggested by reviewer DBkM.
**Table 3: Quantitative results on MS-COCO 2017**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**| **FID**|**Speedup Ratio**|
|--|--|--|--|--|--|--|
| Flux|Flow-matching|TeaCache|19.14|0.216|4.89|2.00|
|||SADA|**29.44**| **0.060**|**1.95**|**2.02**|
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's rebuttal. I raise my score to 3 weak accept.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your updated rating and positive recognition. We are genuinely pleased with your emphasis that our paper is **well-organized** and has **solid theoretical proofs**. We are particularly grateful for your support regarding our objective of training-free acceleration, which maintains **consistency with the original diffusion model**.
Your insightful feedback has encouraged and inspired us to further investigate SADA's potential. We have raised the Adam-Moulton method to third-order, leading to significantly improved generative performance and efficiency compared to previous baselines. Meanwhile, we have verified the superior performance of SADA on state-of-the-art flow-matching models with MM-DiT architecture
We are committed to open-sourcing the SADA plug-in package (diffuser & comfyUI), enabling training-free acceleration of existing diffusion models (and their variants) with just a single line of configuration code.
Thank you again for the time and efforts put in reviewing. Should you have additional questions or suggestions, please do not hesitate to reach out. | Summary: The paper proposes SADA (Stability-guided Adaptive Diffusion Acceleration), a method to accelerate diffusion models by jointly optimizing step-wise and token-wise sparsity using a unified criterion based on the denoised latent \( x_0 \). Key contributions include: (1) alignment of pruning decisions with \( x_0 \)-based solvers for stability, (2) a second-order Adams-Moulton approximation for skipped steps, and (3) a token cache mechanism to mitigate information loss. Experiments on Stable Diffusion 2 and SDXL demonstrate up to 1.52× speedup while maintaining image quality (e.g., LPIPS of 0.118 on SDXL). The method outperforms baselines like DeepCache and AdaptiveDiffusion in metrics such as FID and LPIPS.
Claims And Evidence: The claims are largely supported by experiments, but some aspects need clarification:
- The assertion that \( x_0 \)-based pruning is "more stable" than \( x_t \)-based methods is validated via metrics (Table 1), but direct ablation studies comparing \( x_0 \) vs. \( x_t \) criteria are missing.
Methods And Evaluation Criteria: - **Methods**: Combining step/token pruning via \( x_0 \)-alignment is novel and sensible. The Adams-Moulton approximation and token cache are well-motivated.
- **Evaluation**: COCO-2017, SD2/SDXL, and standard metrics (LPIPS, FID) are appropriate. However, user studies or qualitative examples (beyond Fig. 5) would strengthen claims about preserved visual details.
Theoretical Claims: Overall, the theoretical proof is solid. There are two possible concerns:
- **Theorem 3.1** (global token average): Proof in Appendix A.1 applies Lindeberg-Feller CLT but assumes independent tokens, which diffusion latents may not satisfy?
- **Theorem 3.2** (error bound): The proof assumes Lipschitz continuity of \( \epsilon_\theta \), which is standard but not empirically verified. Or it would be better to have some literature support.
Experimental Designs Or Analyses: - Table 1 shows strong results, but baselines like ToMeSD or concurrent methods (e.g., DiT-FastAttn) are omitted.
- The ablation study (Table 2) reports improved quality with fewer steps. The authors should clarify if this stems from their method’s stability or experimental setup.
Supplementary Material: Reviewed appendices:
- **Appendix A**: Proofs for Theorems 3.1 and 3.2 are detailed but lack empirical validation or literature support of assumptions(e.g., Lipschitz continuity).
- **Appendix B**: Analysis of token merging/pruning as low-pass filters is insightful but needs empirical validation or literature support.
Relation To Broader Scientific Literature: The work builds on diffusion acceleration via step skipping (DPM-Solver++, AdaptiveDiffusion) and token reduction (ToMeSD, DeepCache). It unifies these paradigms, addressing limitations in prior isolated approaches. The \( x_0 \)-alignment aligns with modern ODE solvers (Karras et al., 2022), extending their utility to sparsity decisions.
Essential References Not Discussed: N/A. However, the following works could be included in the related work section or used as baselines to enhance the quality of the paper, as they also focus on training-free acceleration of diffusion models.
- Delta-DiT: A Training-Free Acceleration Method Tailored for Diffusion Transformers
- Faster Diffusion: Rethinking the Role of UNet Encoder in Diffusion Models
- Cache Me if You Can: Accelerating Diffusion Models through Block Caching
Other Strengths And Weaknesses: - **Strengths**: Solid theoretical proof, Novel unification of step/token pruning, strong empirical results, and practical speedup.
- **Weaknesses**: No analysis of computational overhead from the cache mechanism.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Few-Step Improvement: Why does LPIPS improve with fewer steps (Table 2)? Could you provide some insightful explanations?
2. Baseline Comparison: It would be better to add ToMeSD or concurrent methods such as DiT-FastAttn for comparison.
3. Some of the latest diffusion models are trained based on flow matching loss, and whether this method is also suitable for such models.
4. The diffusion model of DiT architecture has also received a lot of attention recently, whether this method is also applicable to this architecture, and if so, increasing the experimental results of this architecture will help to improve the quality of the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's thoughtful feedback and kind support for our work.
Based on the suggestions from Reviewer 4E6r and DBkM, we implement an aggressive version of SADA:
1. Implementing uniform step-wise pruning when the $x_0^t$ trajectory is stable, using Lagrange interpolation.
2. Mitigating degradation by upgrading the Adam-Moulton Approximation from second to third order.
Detailed motivation and formulation are provided in our response to Reviewer 4E6r, and updated results are shown in Table 1.
**Q1: Comparison between $x_0$ and $x_t$-based criterion**
**A1:** We compare our $x_0$ driven paradigm with AdaptiveDiffusion, which leverages the third-order difference of $x_t$ as acceleration criterion. As shown in Table 1, our method consistently delivers superior generation quality—achieving higher PSNR, lower LPIPS and FID—while maintaining a stable speed-up ratio of $\geq 1.8 \times$ regardless of model and scheduler.
The $x_0$ representation is naturally aligned with the final output, capturing essential semantic structures and enabling a more robust criterion than $x_t$.
**Table 1: Comparison between $x_0$ based and $x_t$ based criterion**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**|**FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
| SD2|DPM++|AdaptiveDiffusion| 24.30|0.100| 4.35|1.45|
|||SADA|**26.34**|**0.094**|**4.02**|**1.80**|
|SD2|Euler|AdaptiveDiffusion|21.90|0.173|7.58|**1.89**|
|||SADA|**26.25**|**0.100**|**4.26**|1.81|
|SDXL|DPM++|AdaptiveDiffusion| 26.10| 0.125|4.59|1.65|
|||SADA| **29.36**| **0.084** | **3.51**| **1.86**|
|SDXL| Euler| AdaptiveDiffusion|24.33|0.168|6.11|**2.01**|
|||SADA|**28.97**|**0.093**|**3.76**|1.85|
**Q2 Theoretical claims**
**A2-1 (CLT):** The independence assumption holds for $x_t$ as $\epsilon_t$ is sampled i.i.d. from Gaussian. For $\hat{x}_t=\sqrt{\bar{\alpha}_t}\hat{x}_0^t+\sqrt{1-\bar{\alpha}_t}\hat{\epsilon}_t$, we write $\hat{\epsilon}_t=\epsilon_t+(\hat{\epsilon}_t-\epsilon_t)$. The first term is i.i.d. Gaussian with zero mean by Law of Large Number (LLN). For the second, the training objective $E| \epsilon-\hat{\epsilon}_t|^2$ implies $\hat{\epsilon}_t\to E[\epsilon\mid x_t,t]$, so $E[\hat{\epsilon}_t-\epsilon_t]\to 0$, and by LLN, the sample mean $\overline{\hat{\epsilon}_t-\epsilon_t}\to 0$.
**A2-2 (Lipschiz):** The Lipschiz continuity of $\epsilon_\theta$ is widely assumed by preliminary works such as Adaptive Diffusion and DPM-Solver.
**Q3 Computational overhead**
**a.** *Memory*: For step-wise pruning with third-order Adam-Moulton, after reformulate we only need to store 1 previous $x_0^t$ and 2 previous $dx/dt$ in the cache. For token-wise pruning, we store 1 previous representation $\mathbf{x}^l_t$ for only transformers with the highest resolution. For example, we observe only a neglectable increase in memory usage in the SD-XL model (from 14981 MB to 15127 MB).
**b.** *Complexity*: All computation in the SADA framework is addition and scaling, $O(N)$. Note that SADA does not include any quadratic complexity computation (e.g. cosine similarity, matrix calculation) as in previous works.
**Q4. Qualatative examples & Fewer step generation**
We provide the following link for more generation samples and comparison with previous strategy. In Addition, the CLIP score for generation quality is provided.
https://drive.google.com/file/d/168ovZu9fxcfY5PfE8F5AgkN4la6dvH9f/view?usp=sharing
We appreciate for pointing out the better similarity when decreasing sampling steps. We believe the extent accumulation of error decrease when reducing sampling steps. This trend could be clearly found in our ablation table.
**Q5. Comparison with other token-wise sparisty strategies**
Table 2 shows that our method significantly outperforms ToMeSD. DiTFastAttention is limited to traditional Diffusion Transformer because its windowed attention cannot handle mixed-modality inputs (e.g., MM-DiT modules in SD-3 and Flux). In contrast, our approach easily adapts to these architectures, as demonstrated later.
**Table 2: Quantitative results on MS-COCO 2017**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**| **FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
|SD2|DPM++|ToMeSD|16.29|0.41|13.70|1.10|
|||SADA|**26.34**|**0.094**|**4.02**|**1.80**|
**Q6. SADA for Flow-matching & DiT Architecture**
Under the flow matching objective, the model directly predicts the transportation vector field $dx/dt$ between noise and data distributions. Since the denoising trajectory is ODE-based, our criterion effectively measures its stability. Table 3 on Flux (DiT) shows that our method significantly outperforms the most recent work suggested by reviewer DBkM.
**Table 3: Quantitative results on MS-COCO 2017**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**| **FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
| Flux|Flow-matching|TeaCache|19.14|0.216|4.89|2.00|
|||SADA|**29.44**| **0.060**|**1.95**|**2.02**|
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. My concerns have been mostly addressed. The adaptive mechanism in diffusion models has rarely been studied before and holds great significance; therefore, I consider this work a valuable contribution to the diffusion model community. The additional experimental results provided in the rebuttal further validate the effectiveness of the proposed method. As a result, I am inclined to raise my score.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank you for your thoughtful review and support. We deeply appreciate your recognition of the **novelty and great significance of adaptive mechanisms in diffusion models**, **the uniqueness of dynamic allocation of token-wise and step-wise sparsity**, and **the solid theoretical proof** — which makes our proposed approach accelerate generative modeling by dynamically adjusting configurations for different prompts while best preserving faithfulness.
We are delighted that our additional experimental results and analysis have addressed your concerns. Your constructive feedback is very important for us to refine and improve our approach.
We look forward to releasing the SADA package to the diffusion community in the camera-ready phase! | Summary: The paper proposes SADA, a training-free acceleration method for diffusion models that unifies step-wise (temporal) and token-wise (spatial) sparsity using a stability criterion based on the denoised latent $ x_0 $. Specifically, the paper uses a unified $ x_0 $-guided sparsity criterion for step skipping and token pruning, leveraging $ x_0 $'s structural alignment with modern ODE solvers. A second-order Adams-Moulton method to approximate skipped steps and a token cache to reconstruct pruned tokens. Experiments on Stable Diffusion 2 and XL show speedups of up to 1.5× while maintaining image quality.
## update after rebuttal
Thank you to the authors for their response and additional experiments, which have provided me with a deeper understanding of SADA's effectiveness. However, the baselines compared in this paper are somewhat non-repetitive, and some important papers on cache-based DiT acceleration, such as Learning-to-Cache and $\Delta - Dit$, were not included in the comparison. Additionally, my concerns about the novelty of this paper remain. The caching method proposed in the paper does not differ fundamentally from previous approaches. Although the work most similar to this paper, [1], was published during the review period, earlier works like [2, 3, 4] also bear significant similarity in methodology, especially TeaCache [4]. A comprehensive experimental comparison with these papers, along with a detailed explanation of the differences in approach, is necessary. I still recommend rejecting this paper.
[1] Token-aware and step-aware acceleration for stable diffusion
[2] Cached Adaptive Token Merging: Dynamic Token Reduction and Redundant Computation Elimination in Diffusion Mode
[3] Accelerating diffusion transformers with token-wise feature caching
[4] Timestep Embedding Tells: It's Time to Cache for Video Diffusion Model
Claims And Evidence: - **Claim 1**: $ x_0 $-based pruning improves stability and aligns with solvers.
*Evidence*: Theoretical analysis (Theorem 3.1) links $ x_0 $ to step stability; experiments show lower LPIPS/FID than $ x_t $-based methods (Table 1).
*Problems*: Limited comparison to other $ x_0 $-aligned methods; no ablation on $ x_0 $ vs. $ x_t $.
- **Claim 2**: Unified sparsity outperforms isolated strategies.
*Evidence*: SADA outperforms DeepCache/AdaptiveDiffusion in FID/LPIPS (Table 1).
*Problems*: Missing comparisons to recent works[1,2,3,4]
[1] Token-aware and step-aware acceleration for stable diffusion
[2] Cached Adaptive Token Merging: Dynamic Token Reduction and Redundant Computation Elimination in Diffusion Mode
[3] Accelerating diffusion transformers with token-wise feature caching
[4] Timestep Embedding Tells: It's Time to Cache for Video Diffusion Model
Methods And Evaluation Criteria: - **Methods**: The $ x_0 $-aligned criterion and reconstruction mechanisms are well-motivated. Adams-Moulton provides a principled ODE-based approximation.
- **Evaluation**: COCO-2017 benchmarks with standard metrics (LPIPS, FID) are appropriate. But no clipscore or pick-socre reported, The former evaluated the text alignment of images generated by models after acceleration, while the latter assessed aesthetic scores.
Theoretical Claims: - **Theorem 3.1** (Lindeberg condition): Correct under the assumption of token independence, but real-world spatial correlations in images may affect validity.
- **Theorem 3.2** (Error bound): Relies on Lipschitz continuity of $ \epsilon_\theta $, which is not empirically validated.
Experimental Designs Or Analyses: - **Strengths**: Broad evaluation across schedulers (DPM++, Euler) and models (SD2, SDXL).
- **Weaknesses**:
+ No analysis of computational overhead from the token cache or varying pruning ratios.
+ No clipscore or pick-socre reported, The former evaluated the text alignment of images generated by models after acceleration, while the latter assessed aesthetic scores.
+ Missing comparisons to recent works[1,2,3,4]
+ The acceleration effect obtained is not significant compared to previous work; it's around 1.5x, which is incremental in nature. The ideas presented in this article do not differ significantly from those based on cache methods previously [1,2,3,4], with contributions being incremental as well.
[1] Token-aware and step-aware acceleration for stable diffusion
[2] Cached Adaptive Token Merging: Dynamic Token Reduction and Redundant Computation Elimination in Diffusion Mode
[3] Accelerating diffusion transformers with token-wise feature caching
[4] Timestep Embedding Tells: It's Time to Cache for Video Diffusion Model
Supplementary Material: Reviewed Appendix A (proofs) and B (token merging/pruning analysis). Theorems are logically derived but lack empirical validation of assumptions (e.g., Lipschitz continuity).
Relation To Broader Scientific Literature: Aligns with ODE-based solvers (DPM-Solver++) and token reduction (ToMe). Missing discussion of previous similar work[1,2,3,4]
[1] Token-aware and step-aware acceleration for stable diffusion
[2] Cached Adaptive Token Merging: Dynamic Token Reduction and Redundant Computation Elimination in Diffusion Mode
[3] Accelerating diffusion transformers with token-wise feature caching
[4] Timestep Embedding Tells: It's Time to Cache for Video Diffusion Model
Essential References Not Discussed: The following references should be discussed because they are similar in method to this paper.
[1] Token-aware and step-aware acceleration for stable diffusion
[2] Cached Adaptive Token Merging: Dynamic Token Reduction and Redundant Computation Elimination in Diffusion Mode
[3] Accelerating diffusion transformers with token-wise feature caching
[4] Timestep Embedding Tells: It's Time to Cache for Video Diffusion Model
Other Strengths And Weaknesses: no
Other Comments Or Suggestions: This paper is poorly written and difficult to read.
Questions For Authors: see Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewer for comprehensive comments.
**Q1: Aggressive configuration of SADA**
**A1:** To implement an aggressive version, we leverage the inherent robustness of the per‐step data reconstruction $x_0^t$. When the $x_0^t$ trajectory demonstrates high stability (e.g., the second half of Fig.2), we could employ larger step sizes compensated by higher-order approximations. Building on this insight, we implement a uniform step-wise pruning strategy after the stability of the denoising process with Lagrange interpolation for correction.
For example, consider a 50‐step process. To achieve a step-wise pruning interval of 4 after stable (i.e., compute every 4th step fully and interpolate the skipped steps via Lagrange), we store $\hat{x}_0^t$ every 4 steps before stabilization. Their indices define the fixed-size set $I$, updated dynamically to limit memory usage. For any skipped $t$:
$$
\hat{x}_0^{t}\gets\sum _{i \in I}\prod _{j\in I\setminus \\{ i \\}}\frac{t-t_j}{t_i-t_j}\hat{x}_0^{t_i}
$$
Under this setting, we yield a $\geq 1.8\times$ speedup regardless of models or solvers. To balance the degradation, we raise the Adams-Moulton approximation from second to third order, allowing $x_0^t$ to leverage information from the previous three steps (instead of two), thereby improving numerical accuracy and robustness. Our updated result in Table 1 demonstrates the effectiveness of the above improvements.
**Table 1: Quantitative results on MS-COCO 2017**
|**Model**|**Scheduler**|**Methods**|**PSNR**|**LPIPS**|**FID**|**Speedup Ratio**|
|-|-|-|-|-|-|-|
|SD2|DPM++|DeepCache|17.70|0.271|7.83|1.43|
|||AdaptiveDiffusion|24.30|0.100|4.35|1.45|
|||SADA|**26.34**|**0.094**|**4.02**|**1.80**|
|SD2|Euler|DeepCache|18.90|0.239|7.40|1.45|
|||AdaptiveDiffusion|21.90|0.173| 7.58|**1.89**|
|||SADA | **26.25**|**0.100**|**4.26**|1.81|
|SDXL|DPM++| DeepCache|21.30|0.255|8.48|1.74|
|||AdaptiveDiffusion| 26.10|0.125|4.59|1.65|
|||SADA| **29.36**| **0.084**|**3.51**|**1.86**|
|SDXL|Euler|DeepCache|22.00|0.223|7.36|**2.16**|
|||AdaptiveDiffusion|24.33|0.168|6.11|2.01|
|||SADA|**28.97**|**0.093**|**3.76**|1.85|
**Q2: Comparison between $x_0$ and $x_t$-based criterion**
**A2:** To our best knowledge, we are the first work that considers $x_0$ as acceleration criterion and approximation objective. We compare our paradigm with AdaptiveDiffusion, which leverages the third-order difference of $x_t$, as demonstrated in Table 1.
Residing in an image representation space, $x_0$ demonstrates structural alignment with the final output while evolving in a more robust trajectory (as shown in Fig. 2). It captures semantics and thus yields a more consistent sparsity allocation decision.
**Q3: Comparisons to recent works**
**A3:** We thank the reviewers for listing the four recent works, and we will cite and discuss them in the camera-ready version. The four works explore different Caching mechanisms within diffusion architectures that accelerate sampling. However, we believe our work **fundamentally differs** from the four works listed. Note that [1] is published after submission, which is impossible be addressed at the moment.
**a.** *Methodology*: The four works mentioned above accelerate diffusion in a fixed configuration (e.g., fixed caching interval and pruning ratio), while SADA is adaptive to different prompts. In addition, to our best knowledge, SADA is the first work that unifies token- and step-wise sparsity by a single criterion from the perspective of the ODE-solver process, achieving a multi-granularity adaptive acceleration strategy. The novelty is strongly supported by Reviewer km7j.
**b.** *Motivation*: SADA formulates the acceleration of the ODE-based generative modeling (e.g., Diffusion, Flow-matching) as a **stability measure** of the denoising trajectory, while the four works focus only on the redundancy of the denoising architecture with relatively weak theoretical justification.
**c.** *Experiment*: We believe the objective of post-training acceleration is to preserve the similarity (faithfulness) between original generated and accelerated samples while maximizing speed. Therefore, we evaluate using LPIPS and FID computed between these samples—unlike previous work, which only compares the FID of accelerated samples against the dataset. As shown in Table 2 of our response to Reviewer km7j, our method significantly outperforms [4] on FLUX.1 in terms of faithfulness at the same speed-up ratio.
**Q4: CLIP/Pick Score**
**A4:** Our objective is to preserve the original generation quality through our sparsity framework—metrics like these do not reflect that goal. For completeness, we have provided the requested metrics, along with generation samples and comparisons, via the link below:
https://drive.google.com/file/d/168ovZu9fxcfY5PfE8F5AgkN4la6dvH9f/view?usp=sharing
**Q5: Computational overhead analysis & validation of Theoretical claim**
Please refer to Q2, Q3 in our response to Reviewer km7j. | null | null | null | null | null | null | null | null |
Adapting Precomputed Features for Efficient Graph Condensation | Accept (poster) | Summary: To address the efficiency issue in graph condensation (GC), this paper proposes GCPA, a two-stage framework comprising precomputation and diversity-aware adaptation. The precomputation stage aggregates structural and semantic information for competitive performance, while the adaptation stage refines features via class-wise alignment with minimal cost. Experiments on seven benchmarks confirm its superior efficiency.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: There is no theoretical claims and proofs in this paper.
Experimental Designs Or Analyses: I have reviewed all aspects of the experiment section, including the experimental setup, performance evaluation, efficiency evaluation, transferability evaluation, ablation study, and parameter analysis. Overall, the experimental design and analyses are reasonable. However, some important baselines are missing.
Supplementary Material: I have reviewed all the pages in Appendix.
Relation To Broader Scientific Literature: The contributions of this paper are related to previous studies on graph neural networks (GNN) [1], and data condensation (DC)[2].
[1] Wu, Z., Pan, S., Chen, F., Long, G., Zhang, C., & Philip, S. Y. A comprehensive survey on graph neural networks. TNNLS 2020.
[2] Cui, J., Wang, R., Si, S., & Hsieh, C. J. (2022). Dc-bench: Dataset condensation NeurIPS2022
Essential References Not Discussed: The key contribution of the paper is efficient GC. However, some recent proposed method are not discussed, including SimGC[1], EXGC[2], and CGC[3].
[1] Xiao, Z., Wang, Y., Liu, S., Wang, H., Song, M., & Zheng, T. Simple graph condensation. In ECML-PKDD 2024
[2] Fang, J., Li, X., Sui, Y., Gao, Y., Zhang, G., Wang, K., ... & He, X. (2024, May). Exgc: Bridging efficiency and explainability in graph condensation. In WWW2024
[3] Gao, X., Ye, G., Chen, T., Zhang, W., Yu, J., & Yin, H. (2024). Rethinking and accelerating graph condensation: A training-free approach with class partition. arXiv preprint arXiv:2405.13707.
Other Strengths And Weaknesses: Strength:
1. The paper is generally well-written.
2. The efficiency improvement in GC appears to be significant.
Weakness:
1. The novelty of the paper is poor.
2. A lack of theoratical analysis on why the method is effective.
3. Some important baselines are missing.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. The novelty of the paper is limited. It seems that the structure-precomputation only uses the graph diffusion operators which is widely used to perform message passing, and semantic precomputation is a simple average operation. Could the author further clarify the novelty of this paper.
2. The proposed method appears to be very simple. Could the author provide a theoratical analysis on how the proposed GCPA can achieve comparative or even superior data utility (i.e., classification performance) than the previous GC methods?
3. Why the author do not compare GCPA with recently proposed efficient GC methods, including SimGC[1], EXGC[2], and CGC[3].
[1] Xiao, Z., Wang, Y., Liu, S., Wang, H., Song, M., & Zheng, T. Simple graph condensation. In ECML-PKDD 2024
[2] Fang, J., Li, X., Sui, Y., Gao, Y., Zhang, G., Wang, K., ... & He, X. (2024, May). Exgc: Bridging efficiency and explainability in graph condensation. In WWW2024
[3] Gao, X., Ye, G., Chen, T., Zhang, W., Yu, J., & Yin, H. (2024). Rethinking and accelerating graph condensation: A training-free approach with class partition. arXiv preprint arXiv:2405.13707.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the examination of our work and the thoughtful comments provided. Kindly find our responses to the raised comments and questions below.
**Q1: Some recently proposed efficient GC are not discussed, including SimGC[1], EXGC[2], and CGC[3].**
We thank the reviewer for highlighting the recent efficient GC methods. We set the **smallest condensation ratios** and present **accuracy** with **total running time**. Considering the inconsistent time measurements (e.g., CGC reports only the condensation time), we uniformly run evaluation to measure total running time. Our method consistently outperforms the baselines, while the efficient baselines underperform GEOM. We will revise the manuscript to incorporate these methods. (For fair comparison, we adopt the new baselines’ finer hyperparameter search and update GCPA results accordingly, which slightly differ from those in the paper.)
|Dataset|SimGC|EXGC|CGC|GEOM|GCPA|
|---|---|---|---|---|---|
|Citeseer|73.8 (245s)|69.2 (237s)|72.5 (32s)|73.0 (6,920s)|**75.4** (45s)|
|Cora|80.8 (240s)|82.0 (235s)|82.7 (30s)|82.5 (6,031s)|**82.9** (44s)|
|Arxiv|63.6 (362s)|57.6 (338s)|64.1 (126s)|65.5 (84,356s)|**67.2** (247s)|
|Products|63.3 (4,861s)|62.1 (4,915s)|68.0 (1,093s)|68.5 (1,687,718s)|**69.3** (2,985s)|
|Flickr|45.3 (425s)|47.0 (412s)|46.8 (94s)|47.1 (19,202s)|**47.2** (219s)|
|Reddit|91.1 (702s)|90.2 (692s)|90.6 (182s)|91.1 (100,354s)|**91.3** (505s)|
|AvgDiff|**-2.6**|**-4.2**|**-1.4**|**-0.9**|-|s
**Q2: The novelty of the paper is limited. It seems that the structure-precomputation only uses the graph diffusion operators which is widely used to perform message passing, and semantic precomputation is a simple average operation.**
Our work is motivated by the need to maintain strong structural and semantic guidance from the precomputed features. In many existing methods, precomputed features serve only as **temporary constraints**—initializing the learnable condensed features $Z'$—which can then vanish from the original signal as training progresses. In contrast, our approach employs a **permanent constraint**, where the precomputed features $\hat{X}'$ continuously guide the adaptation: $Z' = f_{adapt}(\hat{X}')$, ensuring their influence remains intact throughout training.
We illustrate this distinction using a variant of GCPA, replacing $f_{adapt}$ with learnable condensed features $Z'$. The performance drop indicate that our permanent constraint is effective in preserving critical information.
||Arxiv|Flickr|
|---|---|---|
|GCPA-Variant (Temporary constraint with learnable $Z'$)|66.9|46.2|
|GCPA (Permanent constraint with learnable $f_{adapt}$ and fixed $\hat{X}'$)|**67.7**|**47.1**|
**Q3: A lack of theoratical analysis on why the method is effective. The proposed method appears to be very simple. Could the author provide a theoratical analysis on how the proposed GCPA can achieve comparative or even superior data utility (i.e., classification performance) than the previous GC methods?**
We appreciate the reviewer’s question and provide theoretical insight below.
**[Under SGC model, graph condensation reduces to feature set condensation]**
In Appendix G, we establish that, for the Simple Graph Convolution (SGC) model, the node embeddings can be precomputed as $X'=(\tilde{D}^{-0.5}\,\tilde{A}\,\tilde{D}^{-0.5})^KX$. Hence, replacing $A$ by an identity adjacency $I$ while using $X'$ is equivalent to using $A$ with the original features $X$. Thus, condensing a graph under SGC is essentially condensing the precomputed features $X'$.
**[Contrastive loss increases mutual information]**
Our contrastive loss uses logistic cross-entropy to distinguish positive (same-class) pairs from negative (randomly sampled) pairs. This is known to maximize a lower bound on $\mathrm{JS}(p^+\|p^-)$, where $p^+$ and $p^-$ are the positive and negative pair distributions. As $\mathrm{JS}(p^+\|p^-)$ increases, $X'$ and the condensed features $Z'$ become more class-discriminative, thereby increasing their mutual information on class-relevant signals. Combined with the SGC equivalence, it follows that condensing $X'$ under this contrastive loss effectively preserves and amplifies the class-relevant information in the original graph features $X$.
To support the claim on the effectiveness of our method, we present KSG mutual information (MI) [a] with accuracies below. The results show a clear increase in mutual information during both stages, along with improved accuracies. This trend highlights the importance of class separation in the adaptation process, thereby contributing to the strong performance of GCPA by helping to preserve class boundaries.
|Stage|Arxiv-MI|Arxiv-Acc|Flickr-MI|Flickr-Acc|
|---|---|---|---|---|
|Precomputation|0.016|64.6|0.011|45.4|
|Adaptation at epoch 10|0.044|65.3|0.016|45.9|
|Adaptation at epoch 50|0.397|66.8|0.148|46.3|
|Adaptation at epoch 100|0.567|67.2|0.347|46.8|
[a] Estimating mutual information | Summary: This paper propose the GCPA method, which not only bring the unbelievable efficiency into the graph condensation process but also gains considerable results, for example, for the Ogbn-products dataset, the conventional trajectory method calls for 452 hours in collecting the trajectories, but the GCPA only cost much less time, while even achieving the SOTA results.
Claims And Evidence: As far as I can see, this paper mainly claims that they achieve better performance with 96x to 2,455x faster than the SOTA methods.
For the evidence, they provide the detailed experiments in Tab. 2, and provide the time comparison in Fig.4.
Methods And Evaluation Criteria: This is what I concern most, because if we only see the individual part of the precomputation stage, each of them seems like a normal step that was widely used in the previous literature. For example, in the CTRL[A], the authors discuss the different ways of initial sets selection. Therefore, from my understanding, the authors just change the expensive matching process to a simple contrastive learning process.
Then, my questions are listed as follow:
If you can ablate the adaptation stage to the other expensive matching processes? Because the precomputation stage seems like a normal trick to me? (I see the experiments on the appendix D, maybe it is associated with my question? But I cannot fully understand them.)
Could you give a deep explanation of the effectiveness of your methods? The current one is more like a technique report, I didn’t see the clear motivation why you use such a precomputation stage and contrastive learning technique?
I am not fully convinced by the story, but I appreciate the simple idea and impressive experiment results. I’ll give the borderline accept for now, and decide later depending on the answer in the rebuttal period.
[A] CTRL: GRAPH CONDENSATION VIA CRAFTING RATIONAL TRAJECTORY MATCHING. Zhang et.al. Arxiv 2023.
Theoretical Claims: I didn’t see any proof.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Yes, but I cannot fully understand the setting of Appendix D.
Relation To Broader Scientific Literature: It is a big innovation since the authors significantly reduce the condensing time but hold considerable results.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. Good results, comprehensive comparsion on addtional PubMed, Products datasets.
Weakness:
1. Not that convincing, just a combination of the data process to me, better inspiration is expected.
Other Comments Or Suggestions: No.
Questions For Authors: See above.
Ethical Review Concerns: No.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the examination of our work and the thoughtful comments provided. Kindly find our responses to the raised comments and questions below.
**Q1: Can you ablate the adaptation stage to the other expensive matching processes? The precomputation stage seems like a normal trick.**
Thank you for the suggestion. We would like to clarify that our framework—precomputation followed by adaptation—is fundamentally different from existing methods, which typically follow an initialize-then-learn paradigm. The key difference lies in where **message passing**—the operation that captures graph structural information—is performed, as shown below:
Existing methods (e.g., CTRL, GEOM):
- Initialization: random sampling, clustering, etc.
- Learning: GNN training with repetitive **message passing** (the main source of computational cost)
Ours:
- Precomputation: one-time **message passing**
- Adaptation: MLP training (without message passing)
Our framework replaces the costly, repeated message passing (in the learning stage) in existing methods with a one-time message passing step (in the precomputation stage), achieving both efficiency and strong performance. This is not just a simple preprocessing trick, and we believe it constitutes a meaningful contribution.
As for replacing adaptation with existing matching processes, such changes may lead to redundant message passing (since precomputation already involves message passing, and existing matching processes involve repeated message passing during learning) and defeat the purpose of our efficiency gains. Nonetheless, we believe it deserves future exploration.
**Q2: I cannot fully understand the setting of Appendix D.**
Thank you for the question. In Appendix D, we highlight the effect of precomputation by comparing two settings:
- GCPA (Ours):
1. Structurally precompute features $H$
2. Semantically precompute condensed features $\hat{X}'$
3. Adapt condensed features $Z'=f_{adapt}(\hat{X}')$ with precomputed features $H$
- GCPA without Precomputation (Ours with Random Initialization):
1. Randomly initialize condensed features $X_{rand}'$,
2. Adapt condensed features $Z'=f_{adapt}(X_{rand}')$ with original features $X$
Table 9 shows that removing precomputation leads to loss of structural information, and hence significantly worse performance. We conclude that precomputation is not merely an initialization step—it plays a critical role by embedding structural information and guiding adaptation learning. This ablation confirms that precomputation meaningfully contributes to performance, beyond what adaptation alone can achieve.
**Q3: A deep explanation of the effectiveness of your methods? Clear motivation why you use such a precomputation stage and contrastive learning technique? Not that convincing, just a combination of the data process to me, better inspiration is expected.**
The two stages–precomputation and adaptation–are motivated by the need to maintain strong structural and semantic guidance from the precomputed features. In many existing methods, precomputed features serve only as **temporary constraints**—initializing the learnable condensed features $Z'$—which can then vanish from the original signal as training progresses. In contrast, our approach employs a **permanent constraint**, where the precomputed features $\hat{X}'$ continuously guide the adaptation: $Z' = f_{adapt}(\hat{X}')$, ensuring their influence remains intact throughout training.
We illustrate this distinction using a variant of GCPA, replacing $f_{adapt}$ with learnable condensed features $Z'$. The performance drop indicate that our permanent constraint is effective in preserving critical information.
||Arxiv|Flickr|
|---|---|---|
|GCPA-Variant (Temporary constraint with learnable $Z'$)|66.9|46.2|
|GCPA (Permanent constraint with learnable $f_{adapt}$ and fixed $\hat{X}'$)|**67.7**|**47.1**|
Besides, we provide theoretical insights on the effectiveness of our method from the perspective of mutual information. We kindly refer to **Reviewer rs1P Q3** for this discussion. | Summary: This paper introduces Graph Condensation via a Precompute-then-Adapt Approach (GCPA), an efficient method for condensing large-scale graphs to accelerate Graph Neural Network (GNN) training. The proposed framework is more computationally efficient than trajectory matching methods and instead consists of two stages: (1) a precomputation stage, which extracts structural and semantic information using a single pass of message passing, and (2) an adaptation stage, which refines the synthetic features using class-wise feature alignment and diversity maximization. The method is evaluated across multiple benchmark datasets, showing up to 2,455× speedup while achieving performance comparable to or better than state-of-the-art (SOTA) graph condensation methods.
## update after rebuttal
As I noted during the rebuttal, I am still concerned about the hyperparameters, and the core contribution driving performance seems relatively straightforward. I will therefore maintain my score.
Claims And Evidence: The authors make strong claims regarding the efficiency of their approach. This claim is backed up well in the paper, e.g., in Figures 2, 4.
Methods And Evaluation Criteria: The authors’ evaluation protocol follows standard practice and aligns with previous research.
Theoretical Claims: The authors don’t provide any theoretical claims.
Experimental Designs Or Analyses: The authors’ experimental design follows standard practice and aligns with previous research.
Supplementary Material: The authors did not provide any supplementary material but have shared an anonymous GitHub repository. However, the files cannot be opened. It is unclear whether this issue is on my end or due to an error from the authors.
Relation To Broader Scientific Literature: The authors include a "Related Work" section that effectively discusses relevant topics.
Essential References Not Discussed: No, I didn't identify any essential references that were missing.
Other Strengths And Weaknesses: **Strengths**:
1. The proposed technique noticeably reduces the time required for the graph condensation process and effectively addresses the issue of repeated training consumption in large-scale graphs for existing structure-free methods, which seems reasonable to me.
2. The proposed technique performs well on benchmark datasets with various condensation ratios, even during initial precomputation.
**Weaknesses**:
1. The method introduces a large number of hyperparameters beyond the standard ones used for training (e.g., hidden dimensions, number of layers, etc.), including:
* $K$ – the number of precomputation hops
* $\alpha$ – the damping factor
* $\beta$ – the residual coefficient
* $\gamma$ – the diversity coefficient
* $M$ – the semantic-based aggregation size
* $S$ – the number of negative samples
However, apart from $\gamma$, the authors do not discuss or demonstrate the effect of these hyperparameters on the method’s performance. This is particularly concerning given the large number of hyperparameters involved.
2. The precomputation stage is mostly without learning, with the exception of Equation 4, where $f_{\text{adapt}}$ operates only on the (updated) node features. I understand how this could be advantageous, but it also introduces certain limitations. Does it truly make sense to coarsen the graph using only non-learnable message passing, with the learning component restricted to (the updated) node features? I appreciate the authors' acknowledgment of this issue and their attempt to address it in the discussion (lines 172–186) via Equation 4. However, this approach still seems somewhat problematic to me.
3. The results, as shown in Table 2 for example, generally surpass the baselines. However, the margin between the best result of the proposed method and the strongest baseline remains relatively small in almost all cases, which makes the method less compelling.
Other Comments Or Suggestions: See questions below.
Questions For Authors: 1. If I understand correctly, the condensed graph has no edges. So why would it make sense to apply a GNN to train on the condensed graph?
2. In Table 3, does the GCN backbone play a role in the condensation process of the proposed method, or is it only relevant to the baselines? If I understand correctly, the condensation is determined by Equations 2, 3, and 4, none of which involve a GNN.
3. In Table 2, I notice that in some cases, the results after the precomputation stage are very similar to those after both stages (precomputation and adaptation). Could you provide some insight into why the adaptation stage appears to have only a minor impact in these cases? Intuitively, I would have expected adaptation to play a more significant role than precomputation.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the examination of our work and the thoughtful comments provided. Kindly find our responses to the raised comments and questions below.
**Q1: Code cannot be opened.**
We apologize for the inconvenience. It appears there was a temporary issue. We have refreshed the repository and it is now accessible.
**Q2: The authors do not discuss the effect of many hyperparameters.**
Thank you for pointing this out. In the extended experiments, we tune the key hyperparameters below on the validation set and analyze their impact:
- Semantic aggregation size $M$
- Negative sample size $S$
- Damping factor $\alpha$
- Precomputation hops $K$
- Residual coefficient $\beta$
The results below show that the model is generally robust to these settings. Some hyperparameters ($M$, $S$) benefit from larger values, while others ($\alpha$) have stable optimal choices. A few others ($K$, $\beta$) require more careful tuning. We will clarify these findings in the revised version.
|$M$|Arxiv|Flickr|
|---|---|---|
|1|66.7|46.8|
|10|66.5|46.6|
|50|66.9|46.9|
|100|67.7|47.1|
|$S$|Arxiv|Flickr|
|---|---|---|
|1|67.0|46.7|
|5|67.7|47.0|
|10|67.7|47.0|
|50|67.7|47.1|
|$\alpha$|Arxiv|Flickr|
|---|---|---|
|0|67.0|45.3|
|0.25|67.7|47.1|
|0.5|66.5|47.0|
|0.75|65.6|47.0|
|$K$|Arxiv|Flickr|
|---|---|---|
|0|64.2|46.9|
|1|65.0|47.0|
|2|67.7|47.0|
|3|63.9|47.1|
|4|63.8|47.0|
|$\beta$|Arxiv|Flickr|
|---|---|---|
|0|66.9|46.4|
|0.25|67.2|47.1|
|0.5|67.1|46.4|
|0.75|67.7|46.3|
**Q3: Does it truly make sense to coarsen the graph using only non-learnable message passing, with the learning component restricted to (the updated) node features?**
Thank you for the thoughtful comment. We agree that relying on non-learnable message passing can introduce limitations and may not generalize to all datasets. However, in many real-world datasets—such as those used in graph condensation benchmarks—non-learnable message passing combined with MLPs (e.g., SIGN [a]) have shown competitive or even SOTA performance. A likely reason is that these benchmark datasets exhibit strong homophily or stable neighborhood patterns, allowing fixed message passing to capture key structural information effectively.
Our method follows a similar principle—non-learnable message passing combined with MLP adaptation—and achieves strong results, suggesting that this design can be effective in practice.
**Q4: The margin between the best result of the proposed method and the strongest baseline remains relatively small in almost all cases.**
Thank you for the observation. Our method is primarily designed for efficiency rather than solely maximizing performance. Given that current SOTA methods can be impractical (e.g., requiring up to 452 hours), our goal is to offer a more efficient alternative while aiming to match, not necessarily surpass, SOTA performance. Notably, our approach achieves significant speedup and even delivers leading results, which we find both promising and encouraging.
**Q5: The condensed graph has no edges, so why would it make sense to apply GNN on it?**
Your are correct that the condensed graph has no edges. This setup was first investigated in SFGC [b], where only self-loops are available for GNN message passing. Although counterintuitive, these methods—including ours—have shown superior performance. A potential reason is that the model learns to encode structural information into the condensed features for GNN to learn effectively, even without edges. We follow this established setting and believe it’s an interesting direction for further investigation.
**Q6: Does GCN backbone play a role in the condensation process of the proposed method?**
You are correct that GCPA does not rely on GCN during condensation. We appreciate your observation and will clarify this in revised version:
- Condensation: All methods except GCPA use GCN to guide learning.
- Evaluation: All methods including GCPA use GCN for evaluation.
**Q7: Why adaptation has only a minor impact in some cases? Intuitively, I would have expected adaptation to play a more significant role than precomputation.**
Thank you for the observation. The impact of adaptation indeed varies in a large range, affected by the quality of the precomputed features, which in turn is influenced by factors like data noises. We illustrate this by adding noise below. When the data is clean, precomputed features are already strong, so adaptation yields modest improvements. When we add noise and degrade the precomputed features, the adaptation becomes much more beneficial.
|$\sigma$ (Gaussian noise)|PubMed (Precomp.)|PubMed (Adapt)|Improve|
|---|---|---|---|
|0|79.7|80.5|+0.8|
|0.01|75.7|77.4|+1.7|
|0.05|57.4|61.4|+4.0|
|0.1|49.8|57.1|+7.3|
|1|42.7|54.4|+11.7|
[a] SIGN: Scalable Inception Graph Neural Networks
[b] Structure-free Graph Condensation: From Large-scale Graphs to Condensed Graph-free Data
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors’ responses and the additional experiments they conducted. However, my concerns regarding the hyperparameters still remain, these experiments over the hyperparameters were only carried out on two datasets, which offers limited validation and is not entirely convincing. Having said that, I understand the constraints of the rebuttal phase and the difficulty of running large-scale experiments in such a short time.
Regarding my concern about the limited impact of the learned adaptation, I find the response not convincing enoug. Demonstrating that adaptation helps when noise is added is kind of expected, given that the adaptation is being learned. This suggests that the precomputation step—while seems pretty trivial—is doing most of the heavy lifting.
To summarize, the precomputation appears to be the most effective part of the proposed method. While the approach may be more efficient, it heavily depends on hyperparameters, which could pose practical challenges in real-world applications.
Therefore, I maintain my score of a weak accept. The paper presents some valuable ideas, but the core contribution that drives performance seems relatively straightforward in my opinion.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate your thoughtful comments and your engagement with us.
**[Addressing Hyperparameter Concerns]**
Thank you for your thoughtful feedback and for acknowledging the additional experiments we provided. We understand and respect your continued concerns regarding the scope of our hyperparameter analysis. Given the constraints of the rebuttal phase, we aimed to provide a representative but manageable set of experiments across two datasets to illustrate the consistency of our method’s behavior. We fully agree that a broader evaluation would strengthen the validation, and we will expand this in the updated version of the paper.
**[Clarifying the Role of the Adaptation Stage]**
Regarding the concern that the adaptation stage might contribute less than the precomputation step, we would like to clarify that while precomputation is indeed a simple and efficient component, it is the adaptation stage that consistently provides meaningful performance gains across a variety of datasets and settings, achieving SOTA performance. We present the quantitative effect of the adaptation stage below:
|Dataset|Ratio|Precomp|Adapt|Gain from Adaptation|
|---|---|---|---|---|
|Citeseer|0.9\%|72.1|75.4|+3.3|
||1.8\%|72.1|74.8|+2.7|
||3.6\%|72.7|74.9|+2.2|
|Cora|1.3\%|80.3|82.1|+1.8|
||2.6\%|80.6|82.9|+2.3|
||5.2\%|80.8|82.3|+1.5|
|PubMed|0.08\%|79.5|80.2|+0.7|
||0.15\%|79.7|80.5|+0.8|
||0.3\%|79.3|81.6|+2.3|
|Arxiv|0.05\%|60.5|67.2|+6.7|
||0.25\%|64.6|67.7|+3.1|
||0.5\%|65.5|68.1|+2.6|
|Products|0.025\%|64.1|69.3|+5.2|
||0.05\%|65.9|69.9|+4.0|
||0.1\%|67.7|71.3|+3.6|
|Flickr|0.1\%|44.4|47.2|+2.8|
||0.5\%|45.4|47.1|+1.7|
||1\%|45.4|47.2|+1.8|
|Reddit|0.05\%|90.5|90.5|+0.0|
||0.1\%|91.3|93.0|+1.7|
||0.2\%|91.4|92.9|+1.5|
|**Mean Diff**|-|-|-|**+2.5**|
As shown, adaptation leads to an average improvement of +2.5\% across datasets and various condensation ratios, indicating a contribution that goes beyond what precomputation alone can offer. In particular, the improvements are more substantial in larger and more challenging datasets (e.g., Arxiv, Products).
We hope these results help clarify the pivotal role of the adaptation stage in our method. We appreciate your recognition of the paper’s efficiency and value, and we thank you again for your constructive comments. | Summary: This paper proposes an efficient graph condensation method composed of aggregation and contrastive learning stages. Extensive experiments indicate that this approach achieves performance comparable to state-of-the-art condensation methods, while significantly improving computational efficiency.
Claims And Evidence: Clearly stated and well-supported.
Methods And Evaluation Criteria: Adequately described and appropriate.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: Requires additional analysis regarding the stability of the proposed method.
Supplementary Material: Provided and satisfactory.
Relation To Broader Scientific Literature: Clearly connects with existing literature on Graph Condensation and Contrastive Learning.
Essential References Not Discussed: No critical omissions identified.
Other Strengths And Weaknesses: ## Strengths
- The proposed method is novel, and the results are robust.
- Significant improvement in efficiency, indicating strong potential for practical applications.
---
## Weaknesses
1. The performance of the GCN on the Citeseer dataset is unexpectedly high (75.4 with a condensed graph versus 71.4 with the original graph), surpassing even the most advanced GNNs on the original Citeseer graph. This anomaly could potentially be attributed to a bug or other underlying issues. Further analysis and discussion are required to clarify this discrepancy.
2. GCPA shows higher variability compared to baselines on datasets like Pubmed and Products, as evidenced by higher standard errors in Table 2. This may stem from naive uniform sampling and inherent instability in contrastive learning. Addressing sampling randomness or imposing additional constraints within the contrastive learning process could help.
3. Some important baselines focused explicitly on efficient graph condensation methods are omitted, notably references [1] and [2]. Including these baselines would strengthen comparative validity. This causes the speed up not convincing, as the proposed method only compare with slowest method though it’s SOTA. It’d better to compare the proposed method with both SOTA and most efficient graph condensation method with acceptable performance.
4. In Line 168, the claim regarding the "non-learning process leading to sub-optimal representations" may not always hold true. For example, some training-free GNNs (e.g., reference [3]) can achieve performance on par with trainingable GNNs. Thus, it is suggested to add more disucssions and clarificaitons on this aspect.
Other Comments Or Suggestions: 1. **Minor Ambiguities:** Figure 2 contains an unclear abbreviation "(SF)." Clarification is needed.
2. **Presentation and Writing Consistency:**
- The term "anchor" appears inconsistently (mentioned only twice in paper and not illustrated explicitly in Figure 3).
- Figure 3’s caption is not organized by different modules, making it difficult to follow.
Questions For Authors: Please see above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the examination of our work and the thoughtful comments provided. Kindly find our responses to the raised comments and questions below.
**Q1: The performance on Citeseer is unexpectedly high, surpassing even the most advanced GNNs on the original Citeseer graph.**
Thank you for your observation. We note that on Citeseer, both baseline methods and our method have shown improved results compared to GCN trained on the original graph. This enhancement is likely due to the condensation process reducing noise in the data. The reproducible code is available [here](https://anonymous.4open.science/r/Precompute-Adapt-Graph-Condensation-6A76/). We note that 75.4 remains within a reasonable range considering recent GNNs achieving 77.5 on Citeseer [a].
|Orig.GCN|GCDM|SFGC|GEOM|GCPA|
|---|---|---|---|---|
|71.4|72.3|72.4|74.3|75.4|
**Q2: GCPA shows higher variability on Pubmed and Products. Addressing sampling randomness or imposing additional constraints within the contrastive learning process could help.**
Thank you for your valuable feedback. To address the instability, we apply constraints including AdamW [b] and L2 regularization to the adaptation model, which constrains the impact of random samples. The updated results are presented below. We will update these changes in the revised manuscript.
| Dataset | Ratio | GCPA (Previous) | GCPA (with AdamW and L2 reg.) |
|---|---|---|---|
|PubMed|0.08\%|80.2±1.9|80.5±0.4|
||0.15\%|80.5±0.8|80.9±0.3|
||0.3\%|81.6±2.4|81.7±0.4|
|Products|0.025\%|69.3±0.2|69.3±0.2|
||0.05\%|69.9±0.7|70.2±0.5|
||0.1\%|71.3±0.7|71.5±0.4|
**Q3: Some important baselines focused explicitly on efficient graph condensation methods are omitted, notably references [1] and [2].**
Thank you for your feedback. We kindly note that the references are missing, so we follow **Reviewer rs1P Q1** to compare with SimGC [c], EXGC [d], and CGC [e]. We set the **smallest condensation ratios** and present **accuracy** with **total running time**. Considering the inconsistent time measurements (e.g., CGC reports only the condensation time), we uniformly run evaluation to measure total running time. Our method consistently outperforms the baselines, while the efficient baselines underperform GEOM. We will revise the manuscript to incorporate these methods. (For fair comparison, we adopt the new baselines’ finer hyperparameter search and update GCPA results accordingly, which slightly differ from those in the paper.)
|Dataset|SimGC|EXGC|CGC|GEOM|GCPA|
|---|---|---|---|---|---|
|Citeseer|73.8 (245s)|69.2 (237s)|72.5 (32s)|73.0 (6,920s)|**75.4** (45s)|
|Cora|80.8 (240s)|82.0 (235s)|82.7 (30s)|82.5 (6,031s)|**82.9** (44s)|
|Arxiv|63.6 (362s)|57.6 (338s)|64.1 (126s)|65.5 (84,356s)|**67.2** (247s)|
|Products|63.3 (4,861s)|62.1 (4,915s)|68.0 (1,093s)|68.5 (1,687,718s)|**69.3** (2,985s)|
|Flickr|45.3 (425s)|47.0 (412s)|46.8 (94s)|47.1 (19,202s)|**47.2** (219s)|
|Reddit|91.1 (702s)|90.2 (692s)|90.6 (182s)|91.1 (100,354s)|**91.3** (505s)|
|AvgDiff|**-2.6**|**-4.2**|**-1.4**|**-0.9**|-|
**Q4: In Line 168, the claim regarding the "non-learning process leading to sub-optimal representations" may not always hold true.**
We acknowledge the misleading claim and revise the paragraph:
Our precomputation stage effectively captures the structural and semantic features of the original graph. Since the precomputation stage is not directly optimized for the final objective, we further integrate an adaptation learning stage that adjusts the class-wise representations.
**Q5: Unclear term "SF".**
Thank you for pointing this out. In Figure 2, "SF" stands for "structure-free", indicating that the condensed graphs possess no edges.
**Q6: Inconsistent term "anchor".**
Thank you for pointing out the inconsistency. To clarify, anchors refer to the sampled features $H_i \in H$, where $H$ denotes the precomputed features. The anchors serve as learning targets during the adaptation stage, preserving the original feature distributions.
**Q7: Figure 3’s caption is not organized by different modules.**
We appreciate your suggestion and revise the caption:
Overview of GCPA framework. (1) *Structure-based precomputation:* Neighborhood aggregation is performed to capture structural dependencies. (2) *Semantic-based precomputation:* Nodes are grouped by semantic relevance using uniformly sampled representations. (3) *Adaptation learning:* Synthetic features v1 and v2 are pushed away through diversity constraints, while v2 and v3 are pushed away through sampled negative pairs.
[a] From cluster assumption to graph convolution: Graph-based semi-supervised learning revisited
[b] Decoupled Weight Decay Regularization
[c] Simple graph condensation, ECML-PKDD 2024
[d] Exgc: Bridging efficiency and explainability in graph condensation, WWW 2024
[e] Rethinking and accelerating graph condensation: A training-free approach with class partition, WWW 2025
---
Rebuttal Comment 1.1:
Comment: If the claim is that recent GNNs can achieve 77+, then it would be helpful to demonstrate that performance using those models as downstream components. For GCN, performance on the original graph is typically around 71.5, while achieving 75 on the condensed graph with the same GCN seems unusual and requires further explanation.
I also took a quick look at the provided code and ran a few tests. I observed the following:
* On Citeseer, the test accuracy was around 72+ and the validation accuracy around 74+, so I was not able to reproduce the reported 74+ or 75+ test performance.
* From the logs, the best epoch appears to be epoch 0 on Citeseer, which might suggest that the proposed learning module isn't having the intended effect in this case.
It would be great to hear more thoughts on these points, or if I might be missing something in the setup.
---
Reply to Comment 1.1.1:
Comment: We appreciate your interest and thoughtful engagement with us.
**[Clarifying Performance Gains from Graph Condensation and advanced GNNs]**
Thank you for your detailed observations and feedback. We would like to clarify the performance gains in our work, highlighting two key aspects:
1. **Graph condensation alone can significantly improve performance.** For instance, GEOM—a prior condensation method—achieves 74.3 on Citeseer using a standard GCN with condensed training data, **without modifying the downstream GCN**. This demonstrates that condensation itself can reduce noise and improve generalization. Our result of 75.4 using GCN on condensed data falls within a reasonable and expected range.
2. **Advanced GNNs achieve even higher accuracy.** As cited, a recent GNN model [a] achieves 77.5 on Citeseer using an entirely different architecture. We reference this to contextualize our results—not to claim superiority, but to show that our method does not exceed the most advanced GNNs, addressing your concern that 75.4 may be unexpectedly high.
Together, these points highlight that graph condensation and advanced GNN architectures are separate approaches—one improves the dataset, the other the model—both offering substantial improvements over original GCN training. While we focus on dataset condensation in this work, we agree that combining them could further enhance performance, and we see this as a valuable direction for future work.
**[Reproducing Results on Citeseer]**
Thank you for your effort in reproducing our results. After reviewing the code, we would like to apologize for the oversight—the `use_test` option was not enabled in the released version by default. This setting is necessary on smaller datasets such as Citeseer, Cora, and PubMed, where the limited training data makes the adaptation process more sensitive.
To illustrate, consider the Citeseer dataset: the training set consists of only 120 nodes (20 per class), resulting in a condensed graph of just 30 nodes (5 per class). However, both structural and semantic precomputations require a larger number of same-class nodes per condensed node (e.g., 10) to effectively capture the distribution and avoid overfitting to a few individual nodes.
To mitigate this limitation, we employ an expert GCN model (with 71.4 accuracy) to generate pseudo-labels. While not necessarily accurate, these labels expand the source signal and support effective adaptation. This process adheres to transductive learning principles and does not introduce label leakage or violate data constraints. Nonetheless, we do not include this setting in the manuscript, as it is a specific mitigation for our learning module on small datasets and becomes negligible on larger ones.
We apologize for any confusion this may have caused. Please use the validated command below to reproduce our results. As noted in our logs below, the method achieves **75.5 ± 0.4** accuracy within 50 epochs, confirming the effectiveness of the proposed learning module.
```
python train.py --dataset citeseer --reduction_rate 0.25 --use_test 1 \
--eval_runs 5 --eval_interval 10 --norm_feat 1 --select_mode random --nlayers_adjust 1 \
--wd_adjust 3e-5 --bn_adjust 1 --hidden_adjust 128 --residual_ratio_adjust 0.7 \
--dropout_adjust 0.3 --dropout_input_adjust 0.7 --lr_adjust 0.0003
```
```
train expert
Epoch: 384, Test acc: 0.715
expert acc: [100.0 73.2 71.5], std: [0.0 0.0 0.0]
eval init
Epoch: 566, Test acc: 0.743
Epoch: 547, Test acc: 0.731
Epoch: 300, Test acc: 0.724
Epoch: 258, Test acc: 0.740
Epoch: 399, Test acc: 0.719
init acc: [74.5 74.2 73.1], std: [4.5 1.3 0.9]
adapt epoch 10
Epoch: 25, Test acc: 0.747
Epoch: 22, Test acc: 0.744
Epoch: 36, Test acc: 0.747
Epoch: 6, Test acc: 0.728
Epoch: 69, Test acc: 0.752
acc: [70.2 76.0 74.4], std: [2.7 0.5 0.8]
adapt epoch 20
Epoch: 75, Test acc: 0.746
Epoch: 13, Test acc: 0.741
Epoch: 28, Test acc: 0.747
Epoch: 34, Test acc: 0.752
Epoch: 5, Test acc: 0.743
acc: [71.0 76.4 74.6], std: [1.6 0.5 0.4]
adapt epoch 30
Epoch: 15, Test acc: 0.755
Epoch: 7, Test acc: 0.748
Epoch: 38, Test acc: 0.751
Epoch: 423, Test acc: 0.760
Epoch: 12, Test acc: 0.748
acc: [70.7 77.2 75.2], std: [1.4 0.3 0.5]
adapt epoch 40
Epoch: 12, Test acc: 0.747
Epoch: 143, Test acc: 0.757
Epoch: 136, Test acc: 0.759
Epoch: 337, Test acc: 0.755
Epoch: 509, Test acc: 0.756
acc: [69.7 77.8 75.5], std: [1.5 0.2 0.4]
adapt epoch 50
``` | null | null | null | null | null | null |
Proxy-FDA: Proxy-based Feature Distribution Alignment for Fine-tuning Vision Foundation Models without Forgetting | Accept (poster) | Summary: The paper introduces Proxy-FDA, a novel feature-space regularization method designed to prevent concept forgetting during the fine-tuning of vision foundation models. The key idea is to align the local structures of pre-trained and fine-tuned feature distributions using nearest neighbor graphs, which is further enhanced by generating synthetic features (proxies) to increase data diversity. Experiments demonstrate that Proxy-FDA significantly reduces concept forgetting across various fine-tuning settings and tasks, including end-to-end fine-tuning, few-shot prompt tuning, continual fine-tuning, and applications beyond classification like image captioning and visual question answering. The method achieves state-of-the-art results in mitigating forgetting, showing a strong correlation between a structure-aware distributional distance metric (OTDD) and concept forgetting.
Claims And Evidence: The claims made in the submission are well-supported by clear and convincing evidence. The authors provide extensive experimental results across multiple datasets and tasks, demonstrating the effectiveness of Proxy-FDA in reducing concept forgetting. They also conduct ablation studies to analyze the impact of different components of their method, such as the feature distribution alignment and proxy generation. The correlation analysis between OTDD and concept forgetting further strengthens the validity of their approach. However, the claim that Proxy-FDA consistently outperforms all other methods across all settings might be slightly overstated, as there could be specific scenarios where other methods perform comparably or better, though the provided evidence strongly supports its general effectiveness.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense for the problem of mitigating concept forgetting during fine-tuning. The use of feature distribution alignment with nearest neighbor graphs captures the local structure of the feature space effectively, and the introduction of synthetic proxies addresses data scarcity issues in few-shot scenarios. The evaluation criteria, including the change in performance on unseen tasks (∆LP) and the distributional distance metric OTDD, are appropriate for assessing the extent of concept forgetting and the quality of feature alignment.
Theoretical Claims: I did not check the correctness of any proofs for theoretical claims in this paper, as the focus is primarily on empirical evaluation and methodological innovation rather than theoretical analysis.
Experimental Designs Or Analyses: The experimental designs and analyses appear sound and valid. The authors conduct experiments on a diverse range of datasets and tasks, ensuring the robustness of their findings. They compare against relevant baselines, including naive fine-tuning, LP-FT, L2SP, and LDIFS, providing a comprehensive evaluation of their method's performance. The ablation studies and sensitivity analyses further validate the effectiveness of individual components and design choices in Proxy-FDA.
Supplementary Material: I reviewed the supplementary material, including the detailed architecture of the proxy generator, the hard class mining strategy, and additional experimental results. These materials provide valuable insights into the implementation details and further support the claims made in the main paper.
Relation To Broader Scientific Literature: The key contributions of this paper are well situated within the broader scientific literature on robust fine-tuning of foundation models. The work builds upon and advances prior research in regularization techniques for fine-tuning, such as L2SP and LDIFS, by introducing a structure-aware feature distribution alignment method. It also relates to knowledge distillation and domain adaptation literature, where preserving and transferring knowledge across different data distributions is a central concern. The use of optimal transport for measuring distributional distances connects to a broader body of work on optimal transport in machine learning.
Essential References Not Discussed: There are no critical references missing from the discussion that would significantly impact the understanding of the paper's contributions. The authors adequately cite and discuss relevant prior work in the areas of fine-tuning, concept forgetting, and related regularization methods.
Other Strengths And Weaknesses: Strengths:
The method is conceptually simple yet effective, leveraging feature space regularization with nearest neighbor graphs and proxy generation.
Extensive experiments across diverse datasets and tasks demonstrate consistent improvements over existing methods.
The analysis of the correlation between OTDD and concept forgetting provides valuable insights into the effectiveness of structure-aware regularization.
Weaknesses:
The computational overhead introduced by the proxy generator could be a limitation in resource-constrained settings.
The method's effectiveness might be sensitive to the choice of hyperparameters, such as the neighborhood size K and the scalar s for proxy generation, though the authors provide some analysis on their sensitivity.
Other Comments Or Suggestions: The paper is well-written and clearly presents the methodology and experimental results.
Questions For Authors: no
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for the recognition of our work and constructive feedback. Below is our response to each concern, as well as new comparisons on compute cost.
**Q1: Sensitivity to hyperparameters like the neighborhood size K and the scalar s for proxy generation**
Given the held-out validation set of each downstream dataset (a reasonable assumption for model fine-tuning), we adjust Proxy-FDA's hyperparameters on that validation set. Fig. 6 shows that results are mostly insensitive to each key hyperparameter in a wide range. We acknowledge there are methods that automatically learn hyperparameters instead of manual tuning, in order to further reduce hyperparameter sensitivity. Examples include meta-learning methods, or recent "validation data-free" methods (e.g., CLAP paper cited in Table 7) that optimize hyperparameters online without even requiring a validation set. Integrating such ideas into Proxy-FDA will be a promising future plan.
**Q2: Computational overhead by the proxy generator could be a limitation in resource-constrained settings**
This concern is related to our hypothetical claims in the 1st paragraph of Section 3.2: despite incurring some computational overhead, proxy feature generation is still compute- and data-efficient (comparatively) to improve data diversity. Other viable strategies like retrieving external data should have higher cost and suffer from distribution shift. After paper submission, we implemented one type of Retrieval Augmented Fine-Tuning (RAFT) method using external data, and the comparison results support the above claims.
Concretely, to enrich both the positive feature set $\mathbf X_{i}^{+}$ and negative set $\mathbf X_{i}^{-}$ (by the amount controlled by scalar $s$), we retrieve top similar samples from the large-scale LAION-400M dataset, instead of synthesizing proxy features \{$\mathbf P_{i}^{+}, \mathbf P_{i}^{-}$\} online. Both methods involve the augmented features (retrieved or synthesized) with FDA loss computation, and we call the methods as RAFT-FDA and Proxy-FDA, respectively.
Note for RAFT-FDA to effectively retrieve external data, the same model is needed to extract features for the sampled batch in $\mathcal D_{\text{ft}}$ and external $\mathcal D_{\text{LAION}}$ to measure their feature similarity. It'd be obviously expensive to use the fine-tuned model to repeatedly refresh all the feature representations of $\mathcal D_{\text{LAION}}$. Hence we use the pre-trained model to pre-compute similarities between the entire $\mathcal D_{\text{ft}}$ and $\mathcal D_{\text{LAION}}$, so each sample in $\mathcal D_{\text{ft}}$ has its external neighbor indices that remain fixed. We treat this as a "pre-processing step" for RAFT-FDA whose training time excludes this step. In each fine-tuning iteration of RAFT-FDA, what requires additional feature extraction using the fine-tuned model is now only a limited number of external data (i.e., indexed neighbors from $\mathcal D_{\text{LAION}}$). Overall, the computational overhead of RAFT-FDA is mainly affected by FDA and external feature extraction/augmentation.
The table below compares RAFT-FDA against Proxy-FDA for few-shot prompt tuning based on CoOp.
| | Proxy-FDA | | RAFT | -FDA | |
|------------------------------------------------|-----------|:-----:|:----:|:-----:|:-----:|
| Percent (%) of augmented features | s | s | 2s | 4s | 6s |
| Avg $\mathcal A_{\text{H}}$ across 11 datasets | 78.13 | 76.02 | 77.1 | 78.29 | **78.84** |
| Training time overhead | **21%** | 58% | 83% | 127% | 171% |
Observations: 1) Proxy generation is data-efficient in the low-data regime. Our Proxy-FDA outperforms RAFT-FDA when the latter retrieves the same or a double amount of external data. Generated proxies achieve higher data efficiency because they adapt to the fine-tuned feature distributions, while using external data will inevitably suffer from distribution shift and provide less effective feature regularization. However, our performance benefits diminish as the size of external data increases (over 4$s$). 2) On the other hand, external data augmentation is costly and the cost increases drastically with the retrieved data size. This is due to the need of extra feature extraction for each external sample using the large vision model. While our proxy generator is lightweight, and can generate proxy features all at once (not individually).
More comments: 1) We may potentially improve RAFT-FDA by feature fusion strategies (e.g., Mixup) to address the distribution shift issue, but the training cost remains high. 2) It's possible to speedup Proxy-FDA through a more efficient architecture design of our proxy generator, which we leave as future work. | Summary: The paper proposes Proxy-FDA, a regularization method for fine-tuning vision foundation models that mitigates concept forgetting by aligning local structural relationships in feature spaces. The core innovation lies in preserving neighborhood structures via nearest neighbor (kNN) graphs derived from pre-trained and fine-tuned features, augmented by dynamically generated proxies to enhance data diversity. By regularizing both neighbor indices and similarity scores, Proxy-FDA transfers rich semantic attributes (e.g., color, texture) encoded in foundation models while adapting to downstream tasks. Extensive experiments on classification, captioning, VQA, and continual learning demonstrate significant reductions in forgetting (quantified via LP and OTDD metrics) compared to point-wise regularization baselines (e.g., LDIFS, L2SP). The method excels in data-scarce settings (e.g., 16-shot tuning) and integrates seamlessly with prompt-tuning frameworks, achieving state-of-the-art performance without compromising downstream accuracy.
## update after rebuttal
Dear authors, I've reviewed your rebuttal. While your responses to some questions, like proxy diversity and hard class mining, show thought, there are gaps. You didn't fully answer on training time and theoretical aspects in - line, just referring elsewhere, which makes it hard for readers. And for 1 - 2 shot tuning results, a summary was lacking. I appreciate your efforts, yet considering these, I'm keeping the “Weak Accept” rating. Revise to make your answers more complete and straightforward.
Claims And Evidence: Supported Claims:
1. Proxy-FDA reduces concept forgetting: Empirical validation across 10+ datasets (Tables 1, 4) and correlation analysis with OTDD (Fig. 3) robustly support this claim. The method consistently achieves higher LP (up to +1.54) than baselines, indicating superior retention of pre-trained knowledge.
2. Proxies enhance feature distribution alignment: Ablation studies (Fig. 7) confirm that proxy generation improves FDA by synthesizing features from underrepresented regions of the data manifold. Comparisons with interpolation-based augmentation (e.g., VOS, NPOS) further validate its effectiveness.
3. Structure-wise alignment outperforms point-wise methods: Proxy-FDA’s use of kNN graphs and similarity transfer (Eq. 2) yields statistically significant gains over LDIFS and L2SP (Tables 1–3), with OTDD analysis (Fig. 3) demonstrating stronger correlation to forgetting than L2 distance.
Unsubstantiated Claims:
1. Proxy diversity and novelty: While proxies are qualitatively shown to represent unseen concepts (Fig. 4), their diversity and novelty lack quantitative metrics (e.g., entropy, coverage).
2. Computational efficiency: Though Proxy-FDA incurs a 17–21% training time overhead (Appendix D), comparisons with retrieval-augmented methods or gradient-based alternatives are absent.
Methods And Evaluation Criteria: Methods: The integration of kNN graph alignment and proxy generation is novel. The use of OTDD, a structure-aware distribution distance, appropriately evaluates alignment quality.
Evaluation:
1. Strengths: Broad validation across tasks (classification, VQA), architectures (CLIP, DINOv2), and settings (end-to-end, continual).
2. Weaknesses: The selection of "other datasets" for ΔLP computation (Table 1) lacks explicit justification (e.g., domain overlap or task relevance).
Theoretical Claims: The paper does not present formal theoretical guarantees. Claims about the superiority of structure-wise alignment are supported empirically but lack proofs (e.g., convergence analysis or generalization bounds). The correlation between OTDD and forgetting is observational, not causal.
Experimental Designs Or Analyses: Strengths:
1. Comprehensive ablations (Fig. 7) isolate contributions of hard class mining, proxy architecture, and similarity transfer.
2. Hyperparameter sensitivity analysis (Fig. 6) validates robustness to batch size and neighborhood size.
Weaknesses:
1. Hard class mining: The heuristic batch construction (Appendix A) is not rigorously compared to alternative strategies (e.g., entropy-based sampling).
2. Extreme low-data regimes: Results for 1–2 shot tuning are omitted, limiting insights into Proxy-FDA’s applicability to ultra-scarce data.
Supplementary Material: The appendices provide critical implementation details:
1.Batch construction (Appendix A): Describes greedy class mining to maximize inter-class similarity.
2.Proxy generator (Appendix B): A lightweight architecture with attention and adaptive pooling (23.6K parameters).
3.OTDD computation (Appendix C): Uses K-means pseudolabels for label-aware distribution alignment.
Relation To Broader Scientific Literature: Proxy-FDA bridges gaps in robust fine-tuning and relational knowledge distillation:
1. Robust Fine-Tuning: Extends LDIFS by replacing point-wise feature matching with structural alignment, akin to graph-based knowledge transfer (Park et al., 2019).
2. Proxy Learning: Differs from metric learning proxies by synthesizing instance-wise features rather than class prototypes.
3. Continual Learning: Outperforms rehearsal-free methods (e.g., DualPrompt) by preserving structural knowledge without task-specific prompts (Table 9).
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Strengths:
1. Practical Versatility: Demonstrated efficacy across vision-language tasks (captioning, VQA) and architectures (ViT, ResNet).
2. Novel Regularization: Combines structural preservation with proxy-augmented diversity, advancing beyond point-wise or logit-based methods.
Weaknesses:
1. Interpretability: The t-SNE visualization (Fig. 4) lacks statistical rigor (e.g., clustering metrics).
2. Scalability: Proxy generation for large-scale models (e.g., ViT-L/14) is not benchmarked.
Other Comments Or Suggestions: Clarity: Eq. 3–4 could be simplified by merging redundant terms.
Questions For Authors: 1. Proxy Diversity: How is the diversity of generated proxies quantified (e.g., feature entropy, pairwise distance)? Could metrics like Fréchet Inception Distance (FID) evaluate synthetic feature quality?
2. Hard Class Mining: Does random batch sampling degrade performance compared to the proposed greedy strategy? If so, by what margin?
3. Computational Trade-offs: How does Proxy-FDA’s training time compare to methods using external data augmentation (e.g., Mixup or retrieval-augmented tuning)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the detailed feedback! Below is our response to the main questions and "weaknesses".
**Q1: Proxy diversity and novelty lack quantitative metrics. Could FID evaluate synthetic feature quality?**
As suggested, many metrics are available to quantify our proxy feature diversity. Also, high proxy diversity often implies a high probability of proxy novelty, especially when the feature distribution is sparsely sampled and has a vast space of unseen data. Hence we focus on quantifying proxy diversity, and the novelty is simply examined through qualitative analysis — for example, one can perform some visual validation by image retrieval (Fig. 4) or even training a decoder on feature representations.
To quantify proxy diversity, we choose the variance loss in Eqs. (3-4), which is widely used in many domains like self-supervised learning to measure feature diversity. Note FID can be used to measure how well our generated proxies maintain the diversity of true features. Our adopted variance loss actually serves a similar purpose, since it is computed in an embedding space that's forced to align with the true one.
Here we report the averaged standard deviation of proxy features in the variance loss: higher value indicates larger diversity. To further aggregate the standard deviation values of the positive and negative proxies, we take their mean and compute its moving average till fine-tuning is completed. The table below compares the aggregated diversity metric of all the proxy generation baselines ablated in Fig. 7.
| | Diversity metric $\times 10^{-2}$ |
|----------------------------|------------------------------------|
| Proxy generation (default) | **3.14** |
| random interpolation | 2.89 |
| VOS | 1.53 |
| NOPS | 1.72 |
Our method clearly achieves higher proxy diversity than VOS/NPOS. The latter two methods focus on outlier synthesis in low-likelihood regions, thus miss the chance to encode diverse unseen data that are crucial for improving FDA. Our method also obtains marginally higher proxy diversity than random interpolation. More importantly, our learning-based method improves diversity in a way that best helps FDA: the diverse proxies not only enrich data but also refine the decision boundary between positive and negative feature manifolds. This is not possible with random interpolation, which explains its lower performance in Fig. 7.
**Q2: Compare Proxy-FDA’s training time with that of retrieval-augmented methods.**
Please refer to our response to Q2 of Reviewer bxDC.
**Q3: Lack theoretical guarantees for FDA. Also, the correlation between OTDD and forgetting is observational, not causal.**
Please refer to our response to Q2 of Reviewer 3vR2.
**Q4: Hard class mining: does random batch sampling degrade performance? Comparing to entropy-based sampling.**
As detailed in Appendix A, our batch sampling is performed by hard class mining plus random data sampling within class. Our ablation studies (Fig. 7) already compare with random batch sampling—the "No hard class mining" baseline—where classes are randomly sampled too. The average $\mathcal A_{\text{H}}$ is compared for few-shot prompt tuning, when we apply Proxy-FDA to CoOp/PromptSRC baselines. We see Proxy-FDA obtains $\mathcal A_{\text{H}}$ of 78.13/80.81 with hard class mining, and 75.23/80.35 with random batch sampling. As mentioned in Appendix E (L800-804), the big performance difference shows the hard class mining is crucial — it samples *close* class distributions, among which we can have meaningful modeling and matching of kNN graphs.
We now compare with the entropy-based batch sampling strategy that is also implemented under our greedy framework in Appendix A (for fair comparison). We simply change the inter-class similarity metric in step 2: our default hard class mining uses FDA loss to select similar class samples, while the entropy-based strategy prioritizes them by low entropy. The entropy-based strategy is found to have moderate decrease in $\mathcal A_{\text{H}}$ (77.46/80.75 vs. 78.13/80.81). This is because entropy cannot characterize similarity adaptively as a function of current *feature distribution structure*. As a result, the batch sampling criterion is decoupled with the structural FDA within sampled batch. While FDA loss-based sampling adapts to the feature distribution structure, and is coupled with FDA-based regularization in batch. Will add the results in paper.
**Q5: Clarifications needed.**
Results for 1–2 shot tuning are shown in Fig. 8 (more details in L860-865).
Table 4 (and L853-857) contains results across different foundation models and architectures (including the large-scale one ViT-L/14), where proxy generation (Proxy-FDA vs. FDA) improves $\Delta_{\text{LP}}$ consistently. | Summary: This paper presents a new approach to mitigate concept forgetting in model fine-tuning (robust fine-tuning) by building on existing feature-matching methods. Specifically, this work aims to align the feature structure by regularizing the feature space using k-nearest neighbors (KNN) within each batch. They also propose generating proxies from the data to preserve diversity across datasets.
Claims And Evidence: Yes. Section 4 is about empirical results.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: There is no theoretical results.
Experimental Designs Or Analyses: Yes. Section 4 is about empirical results. And there are also some empirical details in appendix.
Supplementary Material: The appendix is about some experimental details and supplement results.
Relation To Broader Scientific Literature: This paper is mainly related to model generalization performance, which mainly focusing on the controlling the upper bound of test error, using the information on training error and function class.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths
1. This paper is well-written, which provide a clear statement of the results.
2. There is a strong performance on the new prosed method, which seems reasonable and significant.
Weaknesses
1. There is a lack of discussion about the motivation of the new method. Could you provide more discussion on why such method can improve model performance?
2. There is a lack of theoretical guarantee. Is there some theoretical explanations about the benefits of such method in reducing forgetting?
Other Comments Or Suggestions: See strengths and weaknesses.
Questions For Authors: See strengths and weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for the constructive feedback on our work. Below is our point-by-point response to your questions.
**Q1: Motivation discussion: why Proxy-FDA improves performance.**
(Proxy-)FDA is essentially a feature-space regularization term added to the task loss during model fine-tuning. The goal is to keep the fine-tuned model in the desired vicinity of the pre-trained one, so that the tuned model can preserve pre-trained knowledge while still learning the task at the same time. Extensive experiments show that (Proxy-)FDA can significantly reduce forgetting while achieving strong fine-tuning performance (sometimes better).
For better forgetting mitigation, our high-level idea is to extend existing point-wise feature regularization methods that lack explicit awareness of feature neighborhood structures. Proxy-FDA is proposed to fill this gap - it aligns the structural relations between kNN feature graphs, which is further improved by a proxy feature generator that increases feature diversity. **Two empirical observations** confirm our benefits, and hence reaffirm the motivation behind Proxy-FDA: 1) FDA can transfer the structural knowledge in kNN feature graphs, e.g. visual attribute shared between class concepts (Fig. 4). Preserving such common-sense knowledge is useful to maintain the generalizability of foundation model. 2) There's a strong correlation between forgetting and a structure-aware distributional distance metric OTDD (Fig. 3). Such correlation suggests the need of structure-wise feature regularization in some form to effectively mitigate forgetting, and our structural method Proxy-FDA is one such instantiation. In other words, this observation explains our advantage from an optimization perspective, i.e., optimizing our Proxy-FDA objective is close to optimizing a metric directly related to forgetting.
**Q2: Theoretical explanations of the benefits of Proxy-FDA in reducing forgetting**
Good suggestion. Note the primary focus of this paper is on empirical evaluation of our new method, along with **two empirical observations** (refer to our response to Q1) that shed light on the benefits of Proxy-FDA. However, we argue that it's promising to derive theoretical guarantees based on the 2nd observation that forgetting is strongly correlated with OTDD metric. Interestingly, OTDD is computed in an extremely similar way to our FDA loss -- they both use clustering techniques to account for the clustering structure of the underlying space, and hence both can compare feature distributions with rich geometry awareness. In other words, unlike L2 loss, our FDA loss is a good proxy of a metric (OTDD) that itself is directly related to forgetting. Such finding has two key implications: 1) There exists clear advantage of optimizing FDA loss over L2 loss-based optimization for direct forgetting prevention. 2) More importantly, the generalization error (or forgetting effect) could be bounded by some function of our own distance metric FDA (akin to OTDD). We leave such theoretical analysis for future work.
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's reply. It has addressed my concerns. I will update the score.
---
Reply to Comment 1.1.1:
Comment: Thanks for raising the score! We will integrate the new insights into the paper. | Summary: This paper introduces a novel approach to mitigate concept forgetting during model fine-tuning by extending existing feature-matching methods. The authors propose to preserve feature structure by regularizing the feature space using k-nearest neighbors (KNN) within each batch. Additionally, they develop a method for generating proxies from the data to maintain diversity across datasets.
Claims And Evidence: Yes, the claim has been supported by proposed experimental results
Methods And Evaluation Criteria: Yes. It make sense
Theoretical Claims: No new theory proposed in this paper
Experimental Designs Or Analyses: Some improvement of their experimental results looks marginal. The experimental designs are valid.
Supplementary Material: Yes. Additional experimental results.
Relation To Broader Scientific Literature: The solution is interesting but the broader impact of this work is limited.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
- The research addresses robust fine-tuning, which is a highly active and valuable area with significant practical relevance.
- The approach is well-motivated, with the preservation of data structure during feature matching being both reasonable and innovative.
- The paper is clearly written, making the technical approach accessible and easy to follow.
Weakness:
- Distribution Alignment Method: The motivation for using distribution alignment through feature matching with KNN regularization lacks sufficient justification. The approach bears similarities to knowledge distillation, but the paper doesn't adequately explain how this method differs from distillation between original and fine-tuned models.
- KNN Clustering Limitations: The method clusters features in each batch using KNN, which may not effectively group samples with similar labels, particularly during fine-tuning. The clustering approach could be enhanced with label-based constraints that either include or exclude samples based on label proximity to improve feature alignment.
Other Comments Or Suggestions: NA
Questions For Authors: ## Update After rebuttal
I appreciate the authors' thorough response, which has successfully addressed most of my initial concerns. I will maintain my current score.
For the final version of the paper, I strongly recommend that the authors clearly articulate the fundamental differences between traditional KL based Knowledge Distillation and the proposed FDA method. This distinction should be presented prominently in the main paper to help readers immediately understand the novel contribution.
Thank you for your attention to the review comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for the constructive feedback on our work. Below we include the results of requested experiments, and respond to your specific comments.
**Q1: Justify motivation of using kNN feature-based FDA, and differences from knowledge distillation.**
In response, our introduction section (paragraphs 3 & 4) motivates that we aim to improve over existing feature regularization methods that are often point-wise and preserve limited concepts since they lack explicit awareness of feature neighborhood structures. We propose Feature Distribution Alignment (FDA), a structure-wise regularization method that aligns the structural relations between pre-trained and fine-tuned feature distributions. The structural relations are modeled by feature graphs, and we choose kNN feature graphs because they not only enable efficient graph matching, but also are effective enough to capture the rich knowledge in local feature neighborhoods (e.g. shared visual attribute).
The related work section (L145-152) mentions that Proxy-FDA is indeed similar to Knowledge Distillation (KD), especially to those relational KD methods. Our main difference is that we distill knowledge from both neighbor indices and similarities, with an additional proxy learning component. Appendix G shows Proxy-FDA is directly applicable to KD and is quite performant compared to related KD baselines.
**Q2: Improve FDA by kNN clustering with label constraints**
During our FDA-based fine-tuning, class labels are mainly used in the task loss $\mathcal L_{\text{task}}$, while $\mathcal L_{\text{FDA}}$ is only treated as a feature regularization term without involving labels. The intuition behind the label-free $\mathcal L_{\text{FDA}}$ is that we aim to preserve a foundation model's general knowledge, which can be much richer than class labels on downstream datasets. More specifically, $\mathcal L_{\text{FDA}}$ matches kNN feature graphs to align their structural relations only based on feature (not label) similarities. Fig. 4 shows this can go beyond class concepts in a feature neighborhood with different classes (e.g., cross-class attributes), which is key to maintain the generalizability of foundation models. On the other hand, matching kNN graphs with label constraints may end up aligning class semantics on the downstream task, thus may risk forgetting the general knowledge embedded in foundation models.
In the table below, we empirically compare with an FDA variant that models and matches kNN feature graphs using both feature similarities $\hat w_{ij}$ and label similarities $w_{ij}^t$. Note we use the text encoder of CLIP to compute $w_{ij}^t$ as the text-text similarity between the class templates "a photo of a {class}". Comparisons are performed under the base-to-new setting for few-shot prompt tuning (average across 11 datasets). Results show that the use of $w_{ij}^t$ may produce comparable or better $\mathcal A_{\text{Base}}$ (i.e., fine-tuning accuracy on seen classes), but always leads to much lower $\mathcal A_{\text{New}}$ (i.e., worse generalization on unseen classes - more concept forgetting).
| | $\mathcal A_{\text{Base}}$ | $\mathcal A_{\text{New}}$ | $\mathcal A_{\text{H}}$ |
|-------------------------------------------|----------------------------|---------------------------|-------------------------|
| CoOp | 82.69 | 63.22 | 71.66 |
| +Proxy-FDA ($\hat w_{ij}$ - default) | **83.16** | **73.67** | **78.13** |
| +Proxy-FDA ($\hat w_{ij} \cdot w_{ij}^t$) | 83.02 | 70.91 | 76.49 |
| PromptSRC | 84.26 | 76.10 | 79.97 |
| +Proxy-FDA ($\hat w_{ij}$ - default) | 84.47 | **77.45** | **80.81** |
| +Proxy-FDA ($\hat w_{ij} \cdot w_{ij}^t$) | **84.55** | 77.12 | 80.66 | | null | null | null | null | null | null |
On the Robustness of Reward Models for Language Model Alignment | Accept (poster) | Summary: The paper provides a new theoretical analysis framework to understand the robustness of RM in LLMs.
Claims And Evidence: Yes, I think most of the claims made in the submission clear and convincing.
Methods And Evaluation Criteria: See Questions For Authors part.
Theoretical Claims: I didn't check all the proofs in detail but the theorems provides seem to be reasonable and sounding.
Experimental Designs Or Analyses: Most of the experimental designs are sound and valid. However, there are small points that need to be clarified. See Questions For Authors.
Supplementary Material: I didn't check all the supplementary material in detail.
Relation To Broader Scientific Literature: The paper provides a valuable vision for the current understanding of RM/RLHF robustness.
Essential References Not Discussed: Potentially related works missing:
1. Yan Y, Lou X, Li J, et al. Reward-robust rlhf in llms[J]. arXiv preprint arXiv:2409.15360, 2024.
Other Strengths And Weaknesses: See Questions For Authors.
Other Comments Or Suggestions: 1. line 909: ]
2. Section 3 should be named as "Experiment Settings" as no results are shown in this section.
Questions For Authors: 1. Is there any quantification method to quantify the disjointness between each datasets mentioned in Section3? 
2. Line 184, left column, "Typically, the norm of two vectors ||Wp|| · ||h(x, y)|| largely contributes to maximize the softmax value and cause over-confidence issue, especially in the context of large language models (LLMs) that have large hidden sizes." Can you explain the sentence in detail? What's more, in RM training process, there is no softmax (the language modeling head is replaced by value head), so what is the relationship between this sentence and the context?
3. Is over-confidence the same as overoptimization?
4. For the result in Figure 5(c) and (d), why is the change in the two curves discontinuous despite being caused by the same loss? For example, in RM\_BT, during epoch 2.25-2.5, the curve starts to decline, but during epoch 2.5-2.75, the curve again boosts. Why?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate your suggestions on the typo and the section title. We will make sure to address them in the final version of our paper.
**Q1 - Quantifying disjointness between datasets:** We appreciate the reviewer’s question for disjointness quantification as it would make the splitting criteria clearer. We originally planned on splitting the datasets based on the cosine distances of the embeddings of the prompt and responses. However, due to the diverse split settings outlined in Section 2.2, we were unable to provide a strict quantification rule of thumb for disjointness quantifications.
**Q3 - Over-confidence vs over-optimization:** For clarity, we address the third question before the second one. We view the over-confidence issue, which is originally studied for the conventional multi-class classifiers, as a core cause of the reward model over-optimization problem in the context of reward modeling formulation. [1] shows that an overly growing magnitude of logits triggers classifiers to be over-confident due to the nature of the softmax function. In this paper, we carefully analyze how the backbone model’s hidden state norm is a core cause of the growth in reward magnitude (i.e., which is equivalent to the logit magnitude) as they are a unique type of classifier with two classes but with a single projection head, unlike conventional multi-class classifiers. We continue how over-confidence analysis in RMs connects to over-optimization in Q2.
**Q2 - Clarifications on lines 184-187:** This explanation intends to describe RMs’ formulation as a special case of conventional classifier models, where [1] studies the over-confidence problem, and builds how this over-confidence issue in RM formulation is connected to the over-optimization problem. Reward modeling loss $\mathcal{L}\_\mathrm{BT}$ can be written as a two-class softmax classification. While the over-confidence problem originates from growing logit magnitude in conventional classifiers [1], we are analyzing this problem in the RM context. As the magnitude of the reward (i.e., logit) comes largely from $||h(x, y_||$ by $||W_p|| \simeq 1$ even after training, as we showed, the over-confidence problem in RMs stems from the dispersion of hidden states. As the hidden dimension grows (which is common in larger language models), the norm tends to increase, thereby potentially exacerbating over-optimization issues. This is why these lines of explanation bridge the important connection between the over-confidence and over-optimization issues in RMs.hmm (briefly talked about utilizing embedding model + cosine distance for quantification)
**Q4 - Clarification in Figures 5(c) and 5(d):** Appendix A.3 explains that we used a linear decay scheduler during RLOO training. Consequently, the later phase of training operates with a lower learning rate, which leads to slower parameter updates and a tendency for the model to overfit the prompt over multiple epochs. Moreover, note that the y-axis scales differ between Figures 5(c) and 5(d): Figure 5(c) covers a range of [0.0, 1.0], while Figure 5(d) focuses on [0.85, 1.0] to allow a more fine-grained comparison between the policies trained with $RM_{\text{BT}}$ and $RM_{\text{BT-BSR}}$. In this context, the result can be interpreted as $RM_{\text{BT}}$ stagnating in the later phase of training, reaching about 95% of the maximum reward, while $RM_{\text{BT-BSR}}$ reaches that level by epoch 5. The transient dip and subsequent boost in the curve likely reflect the combined effects of the decaying learning rate and overfitting dynamics, resulting in non-monotonic updates to the proxy reward signal.
**Reference**
[1] Wei, Hongxin, et al. "Mitigating neural network overconfidence with logit normalization." International conference on machine learning. PMLR, 2022. | Summary: This paper investigates the issue of over-optimization in reward models (RMs) within RLHF, identifying excessive hidden state norm dispersion as a key factor. To address this, the authors introduce batch-wise sum-to-zero regularization (BSR), which constrains reward magnitudes by ensuring batch-level zero-centering. They further categorize four generalization scenarios in reward modeling to analyze robustness and over-optimization. Their proposed method outperforms baseline methods and achieves promising experimental results.
Claims And Evidence: Yes
Methods And Evaluation Criteria: The evaluation settings follow (Gao, 2023) to set the synthetic gold RM instead of real datasets with human annotations. This makes sense to do controlled experiments on reward modeling.
Theoretical Claims: No theoretical contents.
Experimental Designs Or Analyses: Yes I checked the evaluation on in-domain, prompt-disjoint, response-disjoint and mutual-disjoint cases. Also I checked the experiments that validates the hypothesis that over-optimization is related to the unconstrained growth of the h(x,y). The design seems reasonable.
Supplementary Material: No
Relation To Broader Scientific Literature: The paper addresses reward hacking problem by adding proper normalization during training, which is orthogonal to prior work that introduces other loss functions (such as penalty in output length [1]).
[1] Chen, Lichang, et al. "ODIN: Disentangled Reward Mitigates Hacking in RLHF." International Conference on Machine Learning. PMLR, 2024.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
1. The paper is very well-written, with each message clearly conveyed in the experimental section.
2. The topic is relevant since reward hacking is a long-standing and unsolved question in the LLM space.
3. The evaluation on in-domain, prompt-disjoint, response-disjoint and mutual-disjoint cases is very useful information.
Other Comments Or Suggestions: None
Questions For Authors: Does the proposed normalization techniques also work for DPO-style methods, where there is no explicit training of a separate reward model?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the insightful comments and will add the suggested paper to the related works.
**Q1 - Normalization techniques to implicit rewards of DAAs**: DAAs use the language model as an implicit reward model, differing from our classifier-based reward models in that they use a sum of log ratios rather than a linear projection. As our normalization, BT-BSR, starts with the solid background on the over-confidence issue that classifiers are prone to, it may not be intuitive to directly apply batch-wise sum-to-zero constraint on implicit RMs. Applying a batch-wise sum-to-zero constraint directly to implicit rewards, which often exhibit negative scales [1], would be counterintuitive.
Nevertheless, over-optimization can also occur with implicit rewards [2], as evidenced by their divergence to negative infinity [3]. As such, divergence is similar to hidden state norm dispersion in our scenario, the straightforward solution could be Z-loss formulation [4,5]:
$$
\mathcal{L}\_{IRM-BSR} = - \lambda \log^2 \sum\_i^{N} \left( \beta \log \frac{\pi\_\theta(y\_{i, w}|x)}{\pi\_\mathrm{ref}(y\_{i, w}|x)} + \beta \log \frac{\pi\_\theta(y\_{i, l}|x)}{\pi\_\mathrm{ref}(y\_{i, l}|x)} \right).
$$
Z-loss is a well-established method for stabilizing large-scale language model pre-training by penalizing divergence in logits. Here, $\mathcal{L}\_\mathrm{IRM-BSR}$ prevents the implicit reward (log-ratio) from diverging to negative values, mirroring how Z-loss regulates the softmax normalizing constant.
We conducted a minimal experiment on Qwen2.5-1.5B trained with TULU3-SFT data [6] comparing plain DPO with DPO plus the $\mathcal{L}\_\mathrm{IRM-BSR}$ regularizer. As shown in Tables A, B, and C, the Z-loss-based regularizer substantially mitigates negative divergence in log-likelihood while preserving training preference accuracy.
| | 0 | 5 | 10 | 15 | 20 | 25 | 30 | 35 | 40 | 45 | 50 | 55 | 60 | 65 | 70 | 75 | 80 | 85 | 90 |
|--------|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|
| DPO | -302| -242| -274| -306| -378| -322| -314| -334| -460| -434| -448| -426| -528| -414| -440| -376| -474| -466| -424|
| DPO+Reg| -249| -260| -270| -292| -340| -296| -251| -304| -366| -384| -364| -344| -378| -320| -356| -306| -392| -388| -324|
> **Table A**: Log-likelihood of chosen responses during training.
| | 0 | 5 | 10 | 15 | 20 | 25 | 30 | 35 | 40 | 45 | 50 | 55 | 60 | 65 | 70 | 75 | 80 | 85 | 90 |
|---|---|---|---|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|-----|
| DPO | -340| -296| -366| -430| -492| -432| -484| -476| -488| -612| -572| -632| -740| -596| -652| -564| -656| -604| -620|
| DPO+Reg| -314| -318| -338| -422| -478| -434| -384| -458| -474| -524| -470| -544| -572| -508| -498| -450| -532| -506| -520|
> **Table B**: Log-likelihood of rejected responses during training.
| | 0 | 5 | 10 | 15 | 20 | 25 | 30 | 35 | 40 | 45 | 50 | 55 | 60 | 65 | 70 | 75 | 80 | 85 | 90 |
|---|---|----|----|---|---|--|---|--|--|--|---|---|-|--|-|---|--|---|-|
| DPO | 0.2125 | 0.375 | 0.5125 | 0.625 | 0.6 | 0.625 | 0.675 | 0.675 | 0.6875 | 0.7125 | 0.6875 | 0.7625 | 0.6999 | 0.7125 | 0.75 | 0.6999 | 0.6625 | 0.75 | 0.675 |
| DPO+Reg| 0.1875 | 0.4 | 0.5375 | 0.6062 | 0.6000 | 0.6687 | 0.6875 | 0.6812 | 0.7437 | 0.6937 | 0.6875 | 0.7312 | 0.8125 | 0.6875 | 0.7437 | 0.6437 | 0.7624 | 0.7812 | 0.7312 |
> **Table C**: Preference accuracy for each batch during training.
**Reference**
[1] Rafailov, Rafael, et al. "From $ r $ to $ Q^* $: Your Language Model is Secretly a Q-Function." First Conference on Language Modeling.
[2] Rafailov, Rafael, et al. "Scaling laws for reward model overoptimization in direct alignment algorithms." Advances in Neural Information Processing Systems 37 (2024): 126207-126242.
[3] Shi, Zhengyan, et al. "Understanding likelihood over-optimisation in direct alignment algorithms." arXiv preprint arXiv:2410.11677 (2024).
[4] Chowdhery, Aakanksha, et al. "Palm: Scaling language modeling with pathways." Journal of Machine Learning Research 24.240 (2023): 1-113.
[5] Wortsman, Mitchell, et al. "Small-scale proxies for large-scale Transformer training instabilities." The Twelfth International Conference on Learning Representations.
[6] Lambert, Nathan, et al. Tulu 3: Pushing frontiers in open language model post-training." arXiv preprint arXiv:2411.15124 (2024). | Summary: This paper explores the challenges of over-optimization in reward models used in RLHF of LLMs. It identifies the dispersion of hidden state norms as a primary cause of over-optimization and proposes batch-wise sum-to-zero regularization (BSR) to address this by penalizing outliers and controlling reward dispersion. The study demonstrates that BSR not only improves the robustness of reward models but also enhances their performance on complex preference prediction tasks across different datasets.
Claims And Evidence: The preliminary theoretical derivation makes sense. However, the claims for different scenarios might need more comprehensive experiments to be robust and convincing.
Methods And Evaluation Criteria: The use of batch-wise sum-to-zero regularization (BSR) in the paper is a sensible approach to addressing over-optimization in reward models by controlling reward dispersion. Nonetheless, the paper’s discussions and experiments lack of focus and the paper is quite hard to read. Various scenarios are considered but for each of them, the experiments are not comprehensive enough (for example consider more models and datasets) to make the results convincing.
Furthermore, it’s important to note that the idea of centering rewards at zero is not entirely novel, as similar concepts have already been explored in existing models (for example see the discussion in [1].
[1] Lambert, N., Pyatkin, V., Morrison, J., Miranda, L. J., Lin, B. Y., Chandu, K., ... & Hajishirzi, H. (2024). Rewardbench: Evaluating reward models for language modeling. arXiv preprint arXiv:2403.13787.
Theoretical Claims: There are some preliminary theoretical derivations which looks correct. There are no technical theoretical claims or proofs.
Experimental Designs Or Analyses: As mentioned above, the experiments are not comprehensive enough and I have concerns about the practical utility of most of the designed evaluation metrics in the discussion.
Supplementary Material: I briefly looked at the appendix.
Relation To Broader Scientific Literature: The key contribution is on the sum-to-zero regularization, but this idea might lack novelty.
Essential References Not Discussed: See above.
Other Strengths And Weaknesses: The exploration of various scenarios and the provision of hypotheses and insights are strengths of the paper.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewer for the comment and would like to further discuss the addressed points.
**W1 - Limited Experimental Results**: Our experimental design can be streamlined into threefold: (1) assessing alignment between proxy RMs and gold RMs with different learning objectives, (2) propagation of over-optimization in RMs to their downstream usage for RLHF training, and (3) understanding real-world impact of such propagation with state-of-the-art model and data. This line of analysis is fully supported with Qwen2.5 and Llama3.2 series with 1B and 3B scale on carefully curated UltraFeedback, followed by Llama-3.1-8B model and 80k Skywork-Preferences dataset. While the clarity in writing could be a valid concern if the logical flow is not fully conveyed, we believe the paper encompasses a large range of models and datasets, especially aligning with practical usage in the research community (e.g., the majority of RMs in RewardBench [1] are based on Llama-3.1 or Llama-3.2 series and Skywork-Preferences dataset).
To ensure that the concerns on the width of experiments, we extend the experiment of Figure 5 (Section 5.2) by scaling the model to Qwen2.5-3B in Table A. This result further validates that the trend shown in Qwen2.5-1.5B on the propagation of RM robustness in the RLHF stage on a larger scale. If the concerns about the clarity of writing can be specified, we would happily provide further explanation and an update in the final version of the paper.
**W2 - Novelty of Batch-wise Sum-to-Zero Constraint in Reward Modeling**: We appreciate the concern on methodological novelty, but there seems to be a major confusion on the zero-centering aspect of BSR. While [1] is cited as the core reference to point out that the idea of centering rewards to zero is not novel, we do not find it to be connected to our approach:
> (Excerpt from Discussion section of RewardBench according to reviewer’s pointer)...Few RMs are Gaussian in their scores across the REWARDBENCH datasets, fewer RMs are centered around 0 reward, and none we tested centered Gaussians. Future work should identify a preferred RM output distribution for downstream RL training.
This is the only part that we find in [1] that mentions centering. However, they intend that RMs are rarely centered through post-hoc analysis. To the best of our knowledge, [2] is the only work that adopts zero-centering *per-prompt*. However, their core motivation lies in the identifiability of RMs, which is distant from ours. We build a solid reason for adopting a *batch-wise* sum-to-zero constraint regarding the mitigation of reward model over-optimization. We would happily incorporate the discussion on [2] for our final version of the paper. However, we emphasize that our method remains novel from its theoretical background and empirical support with varying model sizes, types, and datasets.
| Qwen2.5-3B | Gold Reward Mean | Gold Reward Std |
|:---:|:---:|:--:|
| RM$\_\text{BT}$ | 0.120 | 0.045 |
| RM$\_\text{BT-BSR}$ | **0.123** | 0.045 |
> **Table A**. Qwen2.5-3B-SFT trained with RLOO with each reward model for 5 epochs, evaluated by the gold reward model (ArmoRM). The reward scores are NOT normalized, unlike Figure 5. Unnormalized score of ArmoRM typically ranges around 0.1-0.2 [3]
**Reference**
[1] Lambert, Nathan, et al. "Rewardbench: Evaluating reward models for language modeling." arXiv preprint arXiv:2403.13787 (2024).
[2] Eisenstein, Jacob, et al. "Helping or Herding? Reward Model Ensembles Mitigate but do not Eliminate Reward Hacking." First Conference on Language Modeling.
[3] Wang, Haoxiang, et al. "Interpretable Preferences via Multi-Objective Reward Modeling and Mixture-of-Experts." Findings of the Association for Computational Linguistics: EMNLP 2024. 2024. | Summary: The paper investigates the cause of reward model over-optimization in RLHF and finds that it stems from the increasing variance of the final-layer outputs (hidden states) in the reward model (RM). The authors propose Batch-wise Sum-to-Zero Regularization (BSR) for RM training, which penalizes the second moment of rewards at the batch level. Experiments show that BSR improves RM stability and enhances LLM fine-tuning via RLOO.
Claims And Evidence: The claims are generally well-supported, but some concerns remain:
* The theoretical discussion of BSR in Section 4.2 is unclear. For example, in lines 265–269, the notation $\prec$ is ambiguous. Does it mean $\leq$? If so, considering cases where $r$ is large, should the inequality direction be reversed?
* A misalignment between the hypothesis in Section 4.1 and the proposed method in Section 4.2 appears to exist. Section 4.1 argues that, considering the final-layer computation of $r(x,y) = W h(x,y)$ in the reward model, reward over-optimization occurs due to the increasing variance of $\| h(x,y) \|$ (or $\| h(x,y_w) - h(x,y_l) \|$) while the size of the projection head $W$ remains approximately constant throughout RM training. However, BSR directly penalizes the reward magnitude, which might unnecessarily reduce $W$, contradicting the initial hypothesis. To validate this hypothesis, an additional experiment regularizing $\| h(x,y) \|$ or $\| h(x,y_w) - h(x,y_l) \|$ should be included. Alternatively, if the focus is on BSR itself, Section 4.1 should analyze $r(x,y)$ directly instead of decomposing it into $W$ and $h(x,y)$.
Methods And Evaluation Criteria: The proposed method and evaluation criteria are appropriate for the problem. The use of RM-Bench and Length-Controlled AlpacaEval 2.0 effectively assesses the impact of BSR on reward model stability and RLHF fine-tuning.
Theoretical Claims: The paper does not present a formal theoretical analysis, but its mathematical arguments raise concerns about ambiguity. For instance, the claim of "unconstrained hidden state norm dispersion" may be overstated. In ordinary models (excluding tabular models), the sigmoid function term in the gradient of the BT model should reduce the gradient magnitude as the hidden state norm dispersion increases. Moreover, Figure 2 suggests that the hidden state norm dispersion saturates early.
Experimental Designs Or Analyses: The experimental design is well-structured, and the dataset construction process is appropriate for evaluating the proposed hypothesis and the effect of BSR.
Supplementary Material: I briefly reviewed the supplementary material.
Relation To Broader Scientific Literature: This paper is related to the broader literature on LLM alignment, particularly in addressing reward hacking and reward model over-optimization in RLHF.
Essential References Not Discussed: To the best of my knowledge, there are no essential references missing.
Other Strengths And Weaknesses: One concern is that the performance improvement from the proposed method appears marginal in some evaluations, such as Gold RM evaluation (Figure 5) and RM-Bench (Table 2). The results seem sensitive to hyperparameters and minor experimental settings, raising the possibility that the observed gains could be reversed under slightly different conditions.
Other Comments Or Suggestions: - To better validate the role of BSR in addressing the hypothesis, it would be helpful to show how Figures 1 and 2 change with and without BSR.
- Line 135: Should $D_{\text{KL}}$ be marginalized over $x$?
- Line 185: Should "softmax value" be "reward value"?
Questions For Authors: Table 2 shows a noticeable drop in Easy Acc in RM-Bench when applying BSR. How should this be interpreted? Is there an underlying reason why BSR negatively impacts performance on easier tasks?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s detailed comments. Below, we address each concern:
1. **Claims/Evidence #1 – Notations in Section 4.2**: We regret the confusion from the ambiguous explanations in lines 261–271 and acknowledge that lines 265–269 apply only to a specific case. In the final version, we will include a concise analysis of $\frac{\partial \mathcal{L}\_\mathrm{BSR}}{\partial h(x,y)}$, showing that it introduces a linear penalty on the growing reward scale, which indirectly limits the expansion of $\|h(x,y)\|$. Thus, $\mathcal{L}\_\mathrm{BSR}$ properly complements the BT loss with regularization.
2. **Claims/Evidence #2 – Is BSR properly regularizing the hidden state norms?**: Logit normalization (i.e., $\mathcal{L}\_\text{BT-Norm}$ in Section 4.3) decouples the reward margin from the hidden state norm by dividing the reward by its L2 norm, making the loss scale-invariant [1]. Our analysis in Section 4.1 shows that the reward scale is largely driven by the hidden state norm since $||W_p|| \simeq 1$. However, Figure 4 demonstrates that the strictly normalized loss (RM$_\text{BT-Norm}$) performs substantially worse, suggesting that completely discarding magnitude information removes a valuable discriminative signal for out-of-distribution generalization. In contrast, our BSR method softly regularizes the norm, mitigating over-optimization while preserving useful information. Moreover, Table A shows that even with BSR, the projection head’s norm remains around 1, confirming that the BSR penalty is effectively propagated without fully suppressing the norms.
3. **Theoretical Claims #1 – Ambiguity in “unconstrained norm dispersion”**: We acknowledge that “unconstrained” may not be ideal, given the sigmoid function’s gradient mechanism. Nonetheless, without a proper regularizer like BSR, norm dispersion can be amplified, especially under certain hyperparameter choices (e.g., learning rate), and we have fully demonstrated this throughout the paper. In the final version, we will revise the term to “excessive norm dispersion” or similar.
4. **Strengths and Weaknesses #1 – Generalizability of the Method**: We emphasize that the ultimate evaluation of reward models (RMs) is based on their performance in the RLHF stage. As shown in [2], downstream performance varies significantly with the RM used. Despite marginal improvements in RM benchmarks in some cases, BT-BSR outperforms in the RLHF stage while mitigating verbosity bias [3]—as evidenced by shorter responses and a higher win rate (Table 3). Combined with the improvements seen in RM benchmarks (Figure 4 and Table 2), our regularization method is both generalizable and practically valuable.
5. **Comments or Suggestions #1 – Further Validation for Figures 1 and 2 with BT-BSR**: Table A confirms that $\|W_p\| \simeq 1$ for BT-BSR checkpoints (as shown in Figure 1). Figure 2 empirically supports that the BT loss triggers norm dispersion, while the comparison between Figures 3(a) and 3(b) confirms that BSR effectively mitigates this phenomenon.
6. **Comments or Suggestions #2 – Questions on Notations**: Since $\mathbb{D}\_\mathrm{KL}$ is conditioned on the prompt $x$, both the reward and the KL penalty should be under $x \sim \mathcal{D}$. Additionally, lines 184–188 bridge the over-confidence issue in classic multi-class classifiers to RMs with shared projection heads. (For further details, please refer to our comment on “Q2” for reviewer YT72.) We will clarify these notations in the final version.
7. **Question #1 – Drop in Easy Tasks**: Appendix O of RM-Bench [4] shows that “hard accuracy” has the highest correlation with policy performance ($r=0.45$) while “easy accuracy” is near 0 ($r=0.07$). Although the drop in “easy accuracy” may stem from a compressed representation space due to BSR, it is crucial that “hard accuracy” aligns with actual policy performance after RLHF. Our experiments in Figure 5 and Table 3 confirm that BT-BSR improves outcomes in both controlled and practical settings.
| | **$\| W_p \|$** |
|:--:|:--:|
| **Qwen2.5 (1.5B)** | 0.9884 |
| **Qwen2.5 (3B)** | 0.9933 |
| **Llama-3.2 (1B)** | 0.9896 |
| **Llama-3.2 (3B)** | 0.9905 |
> **Table A**: The norm of the projection head for four different models after reward modeling with BT-BSR.
**Reference**
[1] Wei, Hongxin, et al. "Mitigating neural network overconfidence with logit normalization." International Conference on Machine Learning. PMLR, 2022.
[2] Meng, Yu, Mengzhou Xia, and Danqi Chen. "Simpo: Simple preference optimization with a reference-free reward." Advances in Neural Information Processing Systems 37 (2024): 124198–124235.
[3] Yann Dubois, et al. “Length-controlled alpacaeval: A simple way to debias automatic evaluators.” First Conference on Language Modeling.
[4] Liu, Yantao, et al. "RM-Bench: Benchmarking Reward Models of Language Models with Subtlety and Style." The Thirteenth International Conference on Learning Representations. | null | null | null | null | null | null |
Non-stationary Online Learning for Curved Losses: Improved Dynamic Regret via Mixability | Accept (poster) | Summary: This paper shows that the fixed share algorithm is able to obtain optimal dynamic regret under mixable losses with improper online learning. They also obtain the first gradient variation based dynamic regret bounds under curved losses. The results are novel to the best of my knowledge.
### Post Rebuttal ####
I have read the authors' responses and comments by other reviewers. I think this paper definitely makes a significant progress in dynamic regret literature. I also agree with other reviewers that the presentation of the paper can be greatly improved along with a more coherent discussion regarding prior works.
The comment from authors regarding the applicability of improper to proper reduction under linear / logistic regression is not convincing enough. Note that in this case the availability of covariate before making the prediction allows us to know the gradient of the loss upto a scaling factor. This information along with exp-concavity of losses can be exploited for constructing the reduction.
I believe that a careful revision that addresses the above concerns can greatly benefit the readers and can make the paper more complete and impactful. Based on this, I would like to maintain my score.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Math was not checked in detail.
Experimental Designs Or Analyses: Yes.
Supplementary Material: No
Relation To Broader Scientific Literature: Discussed in the related work of the paper.
Essential References Not Discussed: The authors seem unaware about the following important references. In Table 2, the problems of optimal dynamic regret for proper learning under linear and logistic regression losses were reported to be unsolved. However, they have been addressed affirmatively in the following two papers.
1) Optimal Dynamic Regret in LQR Control, D Baby and YX Wang, NeurIPS 2022 (solves multi-task linear regression)
2) Non-stationary Contextual Pricing with Safety Constraints, D Baby, J Xu and YX Wang, TMLR 2023 (solves general GLM type losses, including logistic regression)
Other Strengths And Weaknesses: See Questions For Authors.
Other Comments Or Suggestions: See Questions For Authors.
Questions For Authors: I believe this paper provides novel insights into a hard problem. My only complaint is that I would like to see a more careful comparison with prior works of Baby and Wang on this topic. This helps to place the current work appropriately in the literature and provides researchers to better understand the pros and cons of each approach.
1) The current work requires to know the form of losses beforehand to compute the output of mixability mapping. Baby and Wang 2021, 2022 do not require to know the form of losses beforehand. Specifically Baby and Wang 2022, requires only access to gradients of the losses.
2) The current work assumes gradient Lipschitnzess for the losses while bounding the comparator gap. I did not see this explicitly stated in any assumptions, but only mentioned in the proof sketch. The work of Baby and Wang 2022 does not require this assumption.
3) Results of Baby and Wang 2021, 2022 can also work with sleeping experts style experts. This reduces the per-round complexity logarithmically. For example, for squared error loss, we obtain a per-round complexity of $O(\log T)$ while blowing the regret up by a logarithmic factor. Does something similar hold true for your approach?
4) In Table 2, I would like to see a comparison regarding run-times as well as the inclusion of prior works that solves the problem of proper learning under linear and logistic regression losses mentioned in the section Essential References Not Discussed above. This way the comparison will be more complete and fair and will directly convey the readers about the merits and demerits of each approach.
5) Are there examples of losses that are mixable but not exp-concave in a compact domain?
I would be happy to see this manuscript accepted in a venue after including the aforementioned details.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thanks for your expert comments! We will address your main concerns regarding the literature comparisons. Without a doubt, Baby and Wang pioneered the line of dynamic regret for exp-concave/strongly convex functions. While we attempted to make a comparison, we unfortunately missed two relevant references, which will be included in the revised version. Moreover, we will add a paragraph discussing the limitations of fixed-share-type methods, which is attached at the end of this rebuttal.
---
**Q1:** "requires to know the form of losses beforehand"
**A1:** Thank you for pointing this out. Yes, constructing the mixability mapping requires focusing on specific loss forms. While this may be a limitation of mixability-based methods, the form of loss is often predetermined in many applications. Examples include online nonparametric regression, online classification, and LQR control, as the reviewer noted. We will clarify this in the next revision
---
**Q2:** "current work assumes gradient Lipschitnzess for the losses"
**A2:** Thank you for the comments. In Theorem 1, we state that $\beta$-smoothness is required to achieve the improved bound. We believe this is a mild assumption, as many curved losses, like those in Section 4, are smooth. That said, removing the smoothness assumption, as done by Baby and Wang et al. (2022), remains a quite interesting question. We will clarify this comparison in the next revision.
---
**Q3:** "Results of Baby and Wang 2021, 2022 can also work with sleeping experts style experts."
**A3**: Currently, achieving $O(\log T)$ time complexity for the fixed-share method is challenging due to the need to add a small portion of the prior distribution $N_0$ at each iteration. We will clarify the time-complexity comparison in the revision.
---
**Q4:** two missing references and comparisons
> - unaware about the following important references...
> - Table 2: comparison regarding run-times as well as the inclusion of prior works.
**A4:** We will definitely include these two papers and update the table to include the time complexity of the compared methods.
$\dagger$ Indicates that the time complexity can be improved to $O(\log T)$ using more refined geometric covering techniques.
| Losses | Method | Regret Bound | Proper Learning | Time Complexity |
| - | -| - |- |- |
| Least-squares loss | Theorem 5 (Baby and Wang, NeurIPS'22) | $\widetilde{O}(d + d^{10/3} T^{1/3} P_T^{2/3})$ | Yes | $O(T)^{\dagger}$ |
| Logistic regression | Theorem 3.1 (Baby et al., TMLR'23) | $\widetilde{O}(d + d^{10/3} T^{1/3} P_T^{2/3})$ | Yes | $O(T)^{\dagger}$ |
---
**Q5:** losses that are mixable but not exp-concave in a compact domain?
**A5:** To our knowledge, common mixable losses, like squared loss, logistic loss are also exp-concave with generally larger coefficients. A key difference is that the mixability coefficient $\eta_{\mathtt{mix}}$ typically does not depend on the diameter of the decision domain $\mathcal{W}$, whereas the exp-concavity coefficient $\eta_{\mathtt{exp}}$ often does. For example, the logistic loss is 1-mixable over $\mathbb{R}^d$ but only $e^{-D}$-exp-concave within a bounded domain $\mathcal{W}$ of diameter $D$. Consequently, mixability-based results may extend to unconstrained comparators, while exp-concavity-based methods generally require bounded domains.
---
[Revision: Section 4.4]
**Limitation and Future Work:** Although our method achieves improved dynamic regret without relying on KKT-based analysis, there remain several directions for improvement. First, regarding time complexity: our method matches the $O(t)$ complexity of Baby and Wang et al. (2021, 2022) for the squared loss. However, prior work can further reduces this to $O(\log T)$ by using the sleeping expert algorithm with a geometric cover, incurring additional multiplicative logarithmic factors in regret. Incorporating this idea into the fixed-share update is a promising direction. Second, while common curved losses like squared loss and logistic regression are smooth, the analysis by Baby and Wang et al. (2022) does not require smoothness. Removing the smoothness assumption in mixability-based analysis remains an interesting theoretical challenge. Finally, to construct the mixable prediction $z_{\mathtt{mix}}$, mixability-based methods require the loss function to have a specific form, unlike the approach by Baby and Wang et al. Although this condition holds in many applications—such as online nonparametric regression, online logistic regression, and LQR control—it is worth exploring whether we can aggregate distributions efficiently using exp-concavity instead of mixability.
---
We will add these discussions and include a fair comparison to Baby and Wang's line of work. Please consider updating the score if our responses and the additions have adequately addressed your concerns. Thank you!
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. I have one more question towards the authors in regards to extension of their results to the setting of proper learning. For the case of linear / logistic regression where the covariate is revealed before making a prediction, could you please comment on what the main blocker is when using the improper-proper online learner reduction that is constructed in Baby, Xu and Wang 2023 (https://openreview.net/pdf?id=fWIQ9Oaao0)?
---
Reply to Comment 1.1.1:
Comment: Thank you for this insightful question. It appears challenging to apply the technique from Baby et al. (2023) to our method, mainly because the source of improper learning differs. In the earlier work (Baby et al., 2021), improper learning is necessary because the method requires learning over an extended box domain. In such a case, the idea of Cutkosky & Orabona (2018) can be used to ensure proper learning by carefully designing the surrogate loss outside of the decision domain.
In contrast, the source of improper learning of our method arises from the aggregation step. As shown in Equations (13) and (15), our prediction could be non-linear. This type of non-linear predictor resembles the one used in the VAW method, and it may be difficult to apply the technique from Baby et al. (2023) to address this issue.
One potential direction is to aggregate distributions using exp-concavity rather than mixability, which may allow for a linear predictor. However, a notable challenge with this approach is that the exp-concavity coefficient may be uncontrolled.
Although proper learning can be achieved in certain interesting cases, the distinction between proper and improper learning remains a key mystery in the study of dynamic regret for curved functions. Exploring methods to achieve proper learning within our framework is an important direction for future work. | Summary: This paper studies non-stationary online convex optimization with mixable loss functions. The class of mixable function includes the exp-concave functions. This paper proposes a fixed-share algorithm for continuous space. In each round, the proposed algorithm requires to obtain a decision satisfying a certain inequality concerning loss function in the round. The paper demonstrates that such a decision can be obtained when the loss function is one of squared, least-squares, or logistic losses. The proposed algorithm achieves $O(d\log T + (d + \log(T / P_T)) T^{1/3}P_T^{2/3})$-dynamic regret, significantly improving existing results with respect to $d$. Furthermore, it offers a simpler and more comprehensible proof compared to previous analyses.
## update after rebuttal
Thank you for your response.
My concerns have been addressed, so I raised my score.
I would like to draw your attention to the fact that the definition of mixable functions will change, so the logarithmic function (example 3) will no longer be an appropriate example.
Claims And Evidence: The paper claims to utilize the concept of mixability for analysis. However, it actually relies on stronger assumptions. Specifically, the proposed algorithm requires $w \in \mathcal{W}$ that satisfies equation (4) for the loss function, which differs slightly from the inequality in the definition of a mixable function (Definition 2). Since Definition 2 deals with distributions whose support is $\mathcal{W}$ and equation (4) handles distributions supported on $\mathbb{R}^d$, it has not been shown that mixable functions always possess $w$ that satisfies equation (4). Moreover, Theorem 1 supposes that the diameter of $\mathcal{W}$ is at most $D$, ensuring these inequalities do not align. Thus, as I understand it, the paper employs mixability-inspired conditions for its analysis rather than direct mixability.
Methods And Evaluation Criteria: The usage of dynamic regret as a performance metric for non-stationary online learning seems appropriate. The analyses indicate that the proposed algorithm achieves near-optimal performance.
Theoretical Claims: I examined the proof sketch for Theorem 1, the proofs of Theorem 3, and Corollaries 1, 2, and 3. In Corollary 1, I am unclear on why $z$, as defined in equation (13), satisfies equation (4), potentially due to omitted critical arguments.
Experimental Designs Or Analyses: There don't appear to be discrepancies in the design or methodology, and they are clearly explained.
Supplementary Material: I reviewed the aforementioned proofs.
Relation To Broader Scientific Literature: While the paper's results are limited to typical exp-concave functions, it achieves near-optimal regret bounds through highly versatile analysis using the conditions inspired by mixability.
Essential References Not Discussed: It appears the necessary prior works have been appropriately cited and discussed to comprehend the contributions.
Other Strengths And Weaknesses: Though the algorithm's optimal performance is restricted to some typical loss functions, the novel ideas and straightforward analysis constitutes a noteworthy contribution. The paper is generally well-written and accessible. However, the paper's connection to mixable functions deserves a more precise discussion.
Other Comments Or Suggestions: - line 78 (right column): meethod -> method
- Eq. (6): N_0(u) -> N_0
- There is inconsistency in the order of arguments in mixed losses. In squared loss, it's denoted as $m(P, y)$, but in least-square loss as $m(y, P)$.
- Proof of Corollary 1
- lines 944-945: inequality (3) -> inequality (4)
- line 945: (3) is essentially -> (13) is essentially
- line 956: give a fixed $z$ -> given a fixed $z$
- Appendix B.3 should be integrated into Appendix A.
Questions For Authors: 1. Could you provide a more detailed proof regarding why equation (13) satisfies equation (4)? Specifically, it is not obvious to me that equation (13) is the optimal solution of the optimization problem defined on line 959.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your very careful review and pointing out two technical problems. We have provided a detailed proof for equation (13), and clarify that our Theorem 1 indeed requires the mixability of loss functions over $\mathbb{R}^d$. These issues will not affect the key contributions of our paper, but we acknowledge that they were not stated with sufficient precision. We will carefully revise the paper to address these imprecisions and ensure clarity.
---
**Q1:** the optimal solution of line 959.
**A1:** Thanks for the detailed inspection of our proof. Here, we provide a more thorough explanation of why equation (13) represents the optimal solution.
*Proof.* First, observe that $m_{sq}(P, y)$ is constant for a given value of $y$. Let us define $M_1 = m_{sq}(P, B)$ and $M_2 = m_{sq}(P, -B)$. The optimization problem in line 959 can then be reformulated as:
$~~~~~~~\begin{equation}\arg\min_{z \in \mathbb{R}^d} \max\\{(z - B)^2 - M_1, (z + B)^2 - M_2\\}.\end{equation}$
Define the functions $g_1(z) = (z - B)^2 - M_1$ and $g_2(z) = (z + B)^2 - M_2$. We have the follow close-form solution for the inner optimzation problem:
$~~~~~~~\begin{equation} h(z) = \max\\{g_1(z), g_2(z)\\} = \begin{cases} g_1(z), \& \text{if } z \leq z_*, \\\ g_2(z), \& \text{otherwise}, \end{cases}\end{equation}$
where $z_* = \frac{M_2 - M_1}{4B}$. We now analyze three separate cases:
1. When $-B \leq z_* \leq B$:
- For $z \in (-\infty, z_*]$, $h(z) = g_1(z)$, which is decreasing since $z_* \leq B$.
- For $z \in [z_*, \infty)$, $h(z) = g_2(z)$, which is increasing since $z_* \geq -B$.
Hence, the minimum of $h(z)$ is achieved at $z = z_*$.
2. When $z_* < -B$:
- On $(-\infty, z_*]$, $h(z) = g_1(z)$ remains decreasing, and the minimum in this interval is at $z = z_*$.
- On $(z_*, \infty)$, the minimum of $h(z)$ is at $z = -B$ since $h(-B) = g_2(-B) = -M_2$.
Under the condition $z_* \leq -B$, one can verify that $h(-B) \leq h(z_*)$, so the overall minimum is attained at $z = -B$.
3. When $z_* > B$: By symmetry to the previous case, the minimum of $h(z)$ occurs at $z = B$ using the same reasoning.
By combining all three cases, we can show that the optimal solution is given in equation (13). We will clarify this reasoning in the revised version of the manuscript. $\blacksquare$
---
**Q2:** ".... it actually relies on stronger assumptions, ...Definition 2..., ...Theorem 1..." ($\mathcal{W}$ versus $\mathbb{R}^d$).
**A2:** Thanks for pointing out this issue. Theorem 1 indeed requires the mixability of loss functions over $\mathbb{R}^d$. We apologize for the confusion caused by the imprecise statements. We now describe the assumptions and decision domain more precisely.
- **On assumption:** Our assumption for Algorithm 1 is that the loss function is mixable over $\mathbb{R}^d$, which is necessary due to the use of a Gaussian prior in the algorithm. This assumption is satisfied by several commonly used curved loss functions in online learning, such as the squared loss and logistic regression loss, as discussed in Examples 1 and 2 and elaborated on in Section 4. Moreover, while the algorithm maintains a distribution over $\mathbb{R}^d$, we emphasize that for certain losses—such as the squared loss—the resulting final predictor $w$ can still lie within the domain $\mathcal{W}$, as shown in Section 4.1.
- **On decision domain:** In the generic algorithmic template, we allow the improper learning where the predictor $\mathbf{w}_t$ is outside the domain $\mathcal{W}$, while the comparator remains constrained within $\mathcal{W}$. Therefore, the proposed method may be improper depending on the loss function. For the squared loss, we obtain a *proper* learning algorithm, but for least-squares regression and logistic regression, the method should be considered *improper*, as discussed in Section 4.
---
To ensure that the assumptions and problem setting are clearly presented for the generic template, we will add a new subsection at the beginning of Section 3 to explicitly state the assumptions and capabilities of the learner. We will add the proofs for equation (13) in the paper.
Please consider updating the score if our responses and the additions in the revised version have adequately addressed your concerns. Thank you! | Summary: This work proposes an algorithm for non-stationary online learning under mixable losses. They provide better dynamic regret bounds in comparison to the existing results in terms of the dependence on the dimension and logarithmic redundancy.
## update after rebuttal
I keep my score which remains positive.
Claims And Evidence: I do not see any problematic claims.
Methods And Evaluation Criteria: I do not see any major issues with the methods.
Theoretical Claims: The proofs seem correct.
Experimental Designs Or Analyses: No numerical experiments.
Supplementary Material: There is no supplementary material.
Relation To Broader Scientific Literature: Improved dynamic regret bounds for mixable or exp-concave losses are valuable for the online learning literature.
Essential References Not Discussed: There does not appear to be missing essential references.
Other Strengths And Weaknesses: While the dynamic regret improvement is a strength, comparisons to the existing literature are a bit lacking. While some comparisons to Baby & Wang, 2021; 2022 are made, they should be discussed in more detail. The proper learning setting should be more clearly discussed and compared. When comparing, altering the regret dependency on dimension $d$ by relying on $L_1$ and $L_2$ norm relation should be more adequately discussed and motivated.
The results appear new and it seems the main idea is to exploit the mixability property as opposed to utilizing the primal and dual variable structure imposed by the KKT conditions. The manuscript would benefit from a more detailed comparison of the proof techniques to further legitimize your claims.
Other Comments Or Suggestions: The paper will benefit from an earlier detailed comparison. I suggest the authors to provide a detailed comparison table in page 2 and move section 4.4 to section 1 as well. The comparison table should extend Table 1, still including the prior works, especially Baby & Wang, 2021; 2022. In addition to specific settings, compare their general regret results as well (possibly using the mixability coefficient). It should also provide differing assumptions if any.
Also, correct the typos such as "mixablity" in lines 204 and 208.
Questions For Authors: What different techniques do you use in comparison to Baby & Wang (2021; 2022) to achieve the improved dynamic regret bounds?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for appreciating the novelty of our methods and for the constructive suggestions. In the revision, we will include a more detailed comparison with Baby and Wang (2021) in the introduction, highlighting the issue of proper learning and the underlying assumptions. Below, we address the questions regarding the differences in proof techniques.
**Q1:** The manuscript would benefit from a more detailed comparison of the proof techniques to further legitimize your claims.
**A1**: Thank you for the helpful comments. Compared with Baby and Wang (2021) and subsequent literature, our work adopts a completely different analytic framework to achieve an improved dynamic regret bound. This distinction is evident in both the algorithmic design and the theoretical analysis.
- *From the perspective of algorithmic design*, the main challenge is how to adapt to non-stationary environments without prior knowledge of $V_T$. Baby and Wang (2021) and the subsequent work address this by employing a strongly adaptive algorithm to ensure adaptivity. In contrast, our method leverages the idea of fixed-share updates over a continuous space. This fundamental difference in algorithmic approach leads to a completely different proof technique in the analysis.
- *On the theoretical side*, the core challenge in Baby and Wang (2021) lies in proving improved dynamic regret for a strongly adaptive algorithm. This requires using KKT conditions to characterize an offline optimal sequence and demonstrating that a strongly adaptive algorithm can track this sequence with low cost. In contrast, our analysis is based on the concept of mixability. By carefully designing the comparator distribution $Q_t$, we are able to directly establish the optimal improved dynamic regret bound.
We will clarify these points in the revision at the introduction level. | Summary: This paper considers online convex optimization (OCO) with mixable stage cost functions. The paper proposesseveral algorithms based on exponential weights with fixed share updates to achieve an improved dynamic regret bound than the bound in (Baby & Wang 2021). The improvements are in two aspects: improvement dependence on dimension d, and a slight improvement on the log(T) term.
Claims And Evidence: This is a technical paper with no simulations. All the theorems and lemmas are clearly supported by proofs.
Methods And Evaluation Criteria: Yes, the proposed method is evaluated by dynamic regret, which is proper and widely used in OCO literature.
Theoretical Claims: The proofs seem correct after a quick read.
Experimental Designs Or Analyses: There is no simulation provided.
Supplementary Material: I went through the proofs in the appendix
Relation To Broader Scientific Literature: This paper considers a different property, mixability, on the OCO stage cost function than the commonly considered convexity and strong convexity. A new algorithm is proposed to leverage this different property.
Essential References Not Discussed: Since the mixability is closely related with strong convexity and one supporting example is quadratic loss which is strongly convex, the paper should also review the dynamic regret analysis for OCO with strongly convex costs, for example [1] discusses the fundamental lower bound of dynamic regret for OCO with strong convexity in Theorem 1.
[1] Li, Y., Qu, G. and Li, N., 2020. Online optimization with predictions and switching costs: Fast algorithms and the fundamental limit. IEEE Transactions on Automatic Control, 66(10), pp.4761-4768.
Other Strengths And Weaknesses: Strengths:
1. The paper explores a different property in the convex functions that enjoy applications in logistic regression. Based on this property, this paper proposes novel algorithms to exploit this property and achieve better dynamic regret bounds.
2. The illustration Figure 1 is helpful for clarity.
3. The discussions on implementation of the proposed algorithms on three specific examples in Section 4 is also very helpful for understanding the paper and implementing the proposed algorithms.
Weaknesses
1. The paper is not very easy to read in general. There is no section for problem formulation, some assumptions and problem settings are in Section 1, some in Section 2, some in Section 3. It is very difficult to read and understand the key setting and the assumptions needed for the proposed algorithm and the regret analysis.
2. Though the paper discusses the implementation of the algorithms in three examples, it is still challenging to see how the algorithm can be implemented for general cost functions, especially the condition (4).
3. There is no simulation provided, casting doubt on the applicability of the proposed algorithms.
4. The paper could benefit from more discussions on the computation complexity of the proposed method, especially when the cost functions are in general form.
Other Comments Or Suggestions: 1. The paper should have a (sub)section devoted to problem formulation, with settings and assumptions in one place and stated explicitly. For example, do you need W to be bounded? Do you need f_t to have some smoothness properties?
2. It is better to provide some overview for the algorithms in all sections. The paper first introduced Algo1, which gives no explanation on implementation issues, and only discusses how to implement it after two sections. It is very confusing for the reader at their first read.
Questions For Authors: See above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for very helpful comments. The main concerns are about i) presentation and ii) technical questions on the construction of mixability prediction for general functions. We first provide a concise answer and will expand the details later.
- **[On Presentation]** Our paper indeed requires much improvement, and we will enhance the presentation according to your constructive suggestions. Specifically, we will: include a subsection for problem formulation, reorganize the presentation of algorithms, and expand on the implementation of key conditions, etc. These changes aim to ensure the paper is easier to read.
- **[On mixability prediction]** For several common functions of interests (like square loss for regression, logistic loss for classification), the mixability prediction can be explicitly and efficiently constructed. For other ones, there may not have a close-form and one can obtain a feasible prediction by solving min-max optimization problems.
---
**Q1:** one paper presentation and assumptions
> - "paper should have a (sub)section devoted to problem formulation"
> - "...do you need W to be bounded? Do you need $f_t$ to have some smoothness properties?"
**A1:** In the original submission, we stated the assumptions within the theorem statements. For Theorem 1, it requires the loss functions to be $\eta$-mixable and $\beta$-smooth, along with the boundedness of the comparator domain. One potential confusion is that we allow *improper* predictions, that is, the predictor $\mathbf{w}_t$ can be unconstrained or take a nonlinear form—such as equations (14) or (15), which are used for least squares and logistic regression.
Thanks for your comments, we will revise the paper to consolidate all assumptions and the problem setting into a separate subsection at the beginning of Section 3 for improved clarify.
---
**Q2:** about algorithm presentation
> "first introduced Algo1, which gives no explanation on implementation issues, and only discusses how to implement it after two sections"
**A2:** The goal of Section 3.1 is to present a generic algorithmic template along with conditions that guarantee improved dynamic regret. However, we agree that deferring the discussion of specific implementations may make the algorithm less accessible. In light of this, we plan to add the following remark in Section 3.1 to provide earlier insight into the implementation:
**[Revision at Section 3.1]**: *Remark 1:* Condition (4) is equivalent to the mixability condition defined in Definition 2, which ensures that for any function that is mixable over $\mathbb{R}^d$, a predictor satisfying condition (4) always exists. In the context of online prediction with a loss function of the form $f_t(\mathbf{w}_t) = \ell(\mathbf{w}_t^\top\mathbf{x}_t, y_t)$, where $(\mathbf{x}_t, y_t)$ is the feature-label pair, Vovk (1999, Equations 11 and 12) and Cesa-Bianchi and Lugosi (2006, Proposition 3.3) provide a general optimization framework for constructing such predictors (which may be improper). Moreover, for the squared loss and logistic loss, closed-form constructions of the predictor are available; these are discussed further in Section 4.
---
**Q3**: about the condition (4)
> - ... it is still challenging to see how the algorithm can be implemented for general cost functions, especially the condition (4)...
>
> - the computation complexity of the proposed method, especially when the cost functions are in general form.
A3: As mentioned in the response to *Q2*, for the online prediction problem where $f_t(\mathbf{w}) = \ell(\mathbf{w}^\top\mathbf{x}_t, y_t)$, Vovk (1999, Equations 11 and 12) and Cesa-Bianchi and Lugosi (2006, Proposition 3.3) provide a general min-max optimization framework for constructing predictions when $\ell$ is a mixable loss function. However, the optimal solution to this optimization problem depends on the specific structure of the loss function.
---
**Q4:** "...there is no simulation provided..."
**A4:** Dynamic regret of curved functions is a very challenging and fundamental theoretical problem in non-stationary online learning, and our primary focus has been on the theoretical aspect. Nonetheless, we are happy to include additional experiments in the revised version to further support our method.
---
**Q5:** the paper should also review the dynamic regret analysis for OCO with strongly convex costs
**A5:** Thanks for bringing this paper to our attention. It studies dynamic regret with switching costs, which is an interesting and complementary direction to our work. We will incorporate a discussion of this paper in the next version.
---
Although the current presentation indeed has certain unclear issues, we believe the core (technical) contributions are interesting and valuable to the community. We will ensure a substantial revision to improve the clarity. Please consider updating the score if these responses have properly resolved your concerns. Thanks! | null | null | null | null | null | null |
Exploiting Similarity for Computation and Communication-Efficient Decentralized Optimization | Accept (poster) | Summary: This paper introduces the Stabilized Proximal Decentralized Optimization (SPDO) method, which achieves state-of-the-art communication and computational complexities within the Proximal Decentralized Optimization (PDO) framework. The authors also propose an accelerated variant (Accelerated-SPDO) based on the Monteiro and Svaiter acceleration method. The paper is well-written, and the proposed algorithms appear promising. Below are detailed comments and suggestions to further improve the paper.
## update after rebuttal
After the rebuttal, the authors promised to add the proof sketch in the camera-ready version and fix the paper to clarify the contribution.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: No
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: This paper addresses key challenges in the literature, particularly in terms of computation and communication efficiency.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
- The paper is well-written, and the proposed algorithms appear promising with rigorous theoretical validation.
Weaknesses:
- The paper would benefit from providing a proof sketch for key theoretical results, particularly for the convergence analysis. This would make the paper more accessible to readers.
- The Accelerated-SPDO algorithm seems to be a straightforward extension of SPDO by incorporating the Monteiro and Svaiter acceleration method. However, are there any unique challenges or modifications required to apply this acceleration in the decentralized optimization setting? If so, these challenges should be highlighted and discussed in detail.
- The experimental section is promising but could be significantly strengthened if including experiments on additional datasets and models to validate the generality of the proposed methods.
Other Comments Or Suggestions: Suggestion:
- In the main body of the paper, the authors first present the non-accelerated SPDO method followed by the accelerated version. However, the contribution bullets list the accelerated method first. To improve clarity and consistency, it would be better to align the sequence of the contribution bullets with the flow of the paper.
Questions For Authors: - Can the proposed SPDO and Accelerated-SPDO algorithms be applicable to nonconvex optimization problems?
- The authors claim that SPDO achieves improved communication complexity compared to existing methods. Can the authors provide more intuition or insight into why SPDO achieves this improvement?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive feedback.
> The paper would benefit from providing a proof sketch for key theoretical results, particularly for the convergence analysis.
Thank you for the suggestion.
We promise to add the proof sketch in the camera-ready version.
> The Accelerated-SPDO algorithm seems to be a straightforward extension of SPDO by incorporating the Monteiro and Svaiter acceleration method. However, are there any unique challenges or modifications required to apply this acceleration in the decentralized optimization setting?
The primary challenge of proposing our methods is that a straightforward combination of Hybrid Projection Proximal-point Method, multiple gossip averaging, and gradient tracking does not work (See the update rule in lines 262-274 and discussion in lines 275-295).
To overcome this, we proposed a carefully designed modification in Algorithm 3 (see the update rule highlighted in blue).
The same modification is also necessary for Accelerated SPDO, which is one of the primary novelties of our paper.
> [...] the contribution bullets list the accelerated method first. To improve clarity and consistency, it would be better to align the sequence of the contribution bullets with the flow of the paper.
Thank you for the suggestion.
We will fix the paper to clarify the contribution.
> Can the proposed SPDO and Accelerated-SPDO algorithms be applicable to nonconvex optimization problems?
PDO, SPDO, and Accelerated-SPDO are designed specifically for convex optimization problems, and their applicability to non-convex optimization is not guaranteed.
However, developing algorithms in the convex case is an important first step for studying algorithms in the more challenging non-convex case.
We believe that our work provides valuable insights that could contribute to the development of future algorithms for non-convex optimization problems.
> [...] Can the authors provide more intuition or insight into why SPDO achieves this improvement?
The main drawback of existing methods, including Decentralized SGD and Gradient Tracking, is that they cannot utilize the multiple local steps.
In their local update, each node performs gradient descent, but fully minimizing the objective function is not desirable.
For Decentralized SGD, [1] showed that we need to decrease the stepsize when we increase the number of local updates to not fully minimize the objective function.
Compared with them, PDO, SPDO, and Accelerated PDO can solve the subproblem in their local update, which leads to lower communication complexities.
## Reference
[1] Koloskova, A., Loizou, N., Boreiri, S., Jaggi, M., and Stich, S. A unified theory of decentralized SGD with changing topology and local updates. In ICML, 2020.
---
Rebuttal Comment 1.1:
Comment: Thanks for your careful response. I have no further question and decide to keep my rating.
---
Reply to Comment 1.1.1:
Comment: Thank you for your valuable feedback. | Summary: This paper studies decentralized optimization, and it proposes several decentralized methods and analyses their convergence. Specifically, they show that their methods achieve the state-of-the-art communication and computation complexity.
Claims And Evidence: The claims are fair.
Methods And Evaluation Criteria: 1. The methods are closely related to two existing works (Scutari & Sun, Li 2020) as discussed in the paper. However, the connection is not clear enough:
- In Page 3, they said that "PDO contains SONATA (Sun et al., 2022) as a special instance when the proximal subproblem is solved exactly. The proofs are deferred to Sec. C and F.2.". I tried to find the explanation of why SONATA is a special case, but didn't find it in Appendix C and F.2.
- In Page 5, it says that "The framework of PDO was initially introduced by Li et al. (2020) and Sun et al. (2022)". However, it's difficult for me to understand their connection when I checked the two references.
2. It is difficult for me to understand the difference between PDO and Stablized PDO. It seems that the update of v in SPDO is simply a gradient descent step with respect to the objective function in the update of x. If so, then $v_i^{(r+1)}$ is also an approximate solution to the minimization problem associated with the update of $x_i$. If this is true, then the novelty and contribution of SPDO will be questionable.
3. The authors should provide more details on the algorithm development. I mean, it is important for the readers to understand the philosophy of the algorithm development and in the current version, it is not easy to understand these methods.
4. Question: In Algorithm 1, the last term in the update of h_i should be $\nabla f_i(x_i^{(r+1)})$ or $\nabla f_i(x_i^{(r)})$? I ask this question mainly because that in gradient-tracking type methods, the updates usually involve old gradients.
5. Typo: In Line 4 of Algorithm 2, it should be $a_j^{(m)}$ rather than $a_j^{(r)}$.
Theoretical Claims: I didn't check the proof. Regarding the theorem itself, the assumption seems to be very strong, and except for affine functions, it is difficult for me to find any other functions that satisfy Assumption 3.
Experimental Designs Or Analyses: Didn't find any issue with the experimental design.
Supplementary Material: It is mainly about proofs and I didn't check it.
Relation To Broader Scientific Literature: Unclear.
Essential References Not Discussed: They mainly discuss gradient-tracking type methods when comparing the computation and communication complexity. I suggest them to also include primal-dual type methods for comparison. To list a few:
[A] S. A. Alghunaim, E. Ryu, K. Yuan, and A. H. Sayed, “Decentralized proximal gradient algorithms with linear convergence rates,” IEEE Trans. Autom. Control, vol. 66, no. 6, pp. 2787–2794, Jun. 2021.
[B] J. Xu, Y. Tian, Y. Sun, and G. Scutari, “Distributed algorithms for com- posite optimization: Unified framework and convergence analysis,” IEEE Trans. Signal Process., vol. 69, pp. 3555–3570, Jun. 2021.
[C] A. Makhdoumi and A. Ozdaglar, “Convergence rate of distributed ADMM over networks,” IEEE Trans. Autom. Control, vol. 62, no. 10, pp. 5082–5095, Oct. 2017.
[D] X. Wu and J. Lu, "A Unifying Approximate Method of Multipliers for Distributed Composite Optimization," in IEEE Transactions on Automatic Control, vol. 68, no. 4, pp. 2154-2169, 2023
The communication complexity of these primal-dual methods are often competitive. For example, the communication complexity of [C] is $O(\frac{\sqrt{\kappa}}{1-\rho})$ where $\kappa$ is the condition number. This communication complexity is competitive compare to that of the non-accelerated methods discussed in Table 1.
Other Strengths And Weaknesses: Discussed above.
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for examining our paper.
> The methods are closely related to two existing works (Scutari \& Sun, Li 2020) as discussed in the paper. However, the connection is not clear enough: [...]
Our paper and existing papers [1,2] use a slightly different notation, which might confuse the reviewer.
We clarify it in the following.
Let define $y_i^{(r)} := h_i^{(r)} + \nabla f_i (x_i^{(r)})$. If we replace $h_i$ with $y_i$ in PDO, we obtain almost the same algorithm as Algorithm 1 shown in [1] as SONATA.
The difference is that PDO solves the subproblem approximately, while SONATA needs to solve it exactly.
Note that the original SONATA [2] has an additional hyperparameter $\alpha$ (See Algorithm 1 in [2]), but as shown in [1], $\alpha$ is not essential, and we can set $\alpha=1$.
Thus, more precisely speaking, PDO contains the original SONATA with $\alpha=1$ as a special instance.
If the reviewer still has concerns, we would appreciate being informed.
We will be happy to resolve them.
> It is difficult for me to understand the difference between PDO and Stablized PDO. [...] If this is true, then the novelty and contribution of SPDO will be questionable.
We respectfully disagree with this reviewer's comment.
Thanks to the update rule of $v$, Stabilized PDO can solve the subproblem more coarsely than PDO (see Eqs. (8) and (9)) and is computationally less expensive.
Specifically, the update rule of $v$ is not a simple gradient descent step.
When $\mu=0$, the update rule of $v$ is $v_i^{(r)} - \frac{1}{\lambda} (\nabla f_i (x_i^{(r+1)}) + h_i^{(r)})$. The gradient is computed at $x$ instead of $v$, and it is not a simple gradient descent.
It plays a crucial role in reducing computational complexity.
> In Algorithm 1, the last term in the update of $h_i$ should be $\nabla f_i(x_i^{(r+1)})$ or $\nabla f_i(x_i^{(r)})$? [...]
Thank you for carefully checking our algorithm.
This is not a typo, and Algorithm 1 is correct.
We wonder if the reviewer might be confused since we use slightly different notations from [1] and [2].
See our response to your first comment.
If the reviewer still has concerns, we would be glad to resolve them.
> Typo: In Line 4 of Algorithm 2, it should be $a_j^{(m)}$ rather than $a_j^{(r)}$.
Thank you for pointing this out.
We will fix it in the revised manuscript.
> Regarding the theorem itself, the assumption seems to be very strong, and except for affine functions, it is difficult for me to find any other functions that satisfy Assumption 3.
We would respectfully disagree with this reviewer's comment.
**All of our theorems, Theorems 1-6, use only Assumptions 1, 2, and 4 and do not use Assumption 3.**
As we explained in lines 120-126, the existing methods, SONATA and Accelerated SONATA, used Assumption 3, while our proposed methods and theorems successfully omit Assumption 3. Instead of using Assumption 3, we use Definition 1. As we mentioned in Remark 1, Definition 1 is not an assumption since **all $L$-smooth functions satisfy Eq. (3) with $\delta \leq 2 L$.**
We can check this by the following inequalities:
\begin{align*}
\frac{1}{n} \sum_{i=1}^n \| \nabla h_i(x) - \nabla h_i (y)\|^2
\leq 2 \| \nabla f (x) - \nabla f(y)\|^2 + \frac{2}{n} \sum_{i=1}^n \| \nabla f_i(x) - \nabla f_i (y)\|^2 \leq 4 L^2 \| x - y\|^2
\end{align*}
> [...] I suggest them to also include primal-dual type methods for comparison.
Thank you for your suggestion.
The papers the reviewer mentioned [A,B,C,D] do not utilize the similarity $\delta$. Thus, our proposed methods, PDO, Stabilized PDO, and Accelerated-PDO, can achieve better communication complexity by utilizing the similarity of local functions, especially when $\delta \ll L$.
We will cite the papers the reviewer mentioned and add the discussion in the revised manuscript.
We believe these additions clarify the relationship between existing and our proposed methods, strengthening our paper.
Therefore, we kindly ask the reviewer to reassess their score. If further concerns remain, we are happy to address them.
## Reference
[1] Tian, Y., Scutari, G., Cao, T., and Gasnikov, A. Acceleration in distributed optimization under similarity. In AISTATS, 2022.
[2] Sun, Y., Scutari, G., and Daneshmand, A. Distributed optimization based on gradient tracking revisited: Enhancing convergence rate via surrogation. In SIAM Journal on Optimization, 2022. | Summary: The paper studies decentralized optimization where multiple nodes, each holding a local function f_i, aim to minimize the average f(x) = \tfrac{1}{n}\sum_i f_i(x). Traditional decentralized methods are constrained by communication overhead and data heterogeneity. The authors propose a Proximal Decentralized Optimization (PDO) framework that leverages (1) a proximal-point formulation (improving upon naive gradient-based updates) and (2) a refined measure of local function similarity (replacing reliance on the worst-case delta_{\max} with an average \delta).
To handle large models realistically, they introduce two variants:
1. Stabilized-PDO (SPDO)– A “stabilized” method that relaxes the requirement for exact subproblem solutions, ensuring that even inexact local solves yield competitive global convergence rates.
2. Accelerated-SPDO – Extends the above approach with an acceleration scheme (inspired by Monteiro–Svaiter) and faster gossip averaging, targeting improved communication complexities in both convex and strongly convex settings.
Claims And Evidence: 1. The authors do not measure or estimate 𝛿 (the second-order similarity measure) directly on these data splits, so the link between “Dirichlet 𝛼” and actual functional similarity is inferred but not verified.
2. The paper does not compare the cost of multiple gossip rounds vs. direct use of a more advanced averaging approach (like exponentiated gradient-based gossip). Hence, the evaluation partly relies on a simplified measure of “communication rounds” that may not reflect real overhead in heterogeneous network conditions.
3. The authors do not show error bars or repeated runs to reveal the variance. If the approach can converge quickly in a median sense but sometimes fails or stalls, that variability matters.
4. Real distributed environments might have node-level heterogeneity in CPU/GPU power. The paper’s simple model (uniform local iteration cost) might mask how well the proposed method handles uneven computation resources.
5. They do not evaluate generalization or test accuracy on complex tasks, even though logistic regression on MNIST is at least somewhat classification-driven. Since they focus on the training objective, it remains unclear whether the improved convergence speed translates to superior test-time performance or any difference in model quality for real tasks.
Methods And Evaluation Criteria: 1. The paper focuses on scenarios where nodes each hold unique local data and where communication is expensive (ring, mesh, or general sparse networks). The proposed proximal-point-based methods (Inexact-PDO, SPDO, Accelerated-SPDO) are appropriate because they are designed to exploit partial overlap or “similarity” among local data while mitigating the high cost of frequent parameter exchanges.
- **Proximal Decentralized Framework**: The premise that each node solves a proximal subproblem (to reduce the discrepancy introduced by local data differences) matches well with the objective of improving the method’s tolerance to data heterogeneity. By explicitly modeling subproblem accuracy, the approach is well-suited for large-scale problems where exact solutions would be prohibitive.
2. **Evaluation Criteria in Experiments**
- **Communication Cost vs. Computation Cost**: The paper measures success primarily through (i) *communication rounds* needed to achieve a target accuracy and (ii) total *local gradient steps* or “computation.” These criteria are standard in the literature for decentralized and federated settings, where the ratio of communication time to local computation time can be crucial.
- **Choice of Datasets**: MNIST is typical for small-scale proof-of-concept experiments, and the authors artificially control heterogeneity (via the Dirichlet parameter \(\alpha\)), which *does* illustrate how the algorithms handle varying levels of data similarity. Although it is limited in scope, it still effectively shows the benefit of reduced communication for more homogeneous local data.
- **Metric of Accuracy**: The authors primarily track objective function decrease or gradient-norm decrease as a function of both communication and computational steps, consistent with standard optimization benchmarks.
3. **Potential Gaps or Areas for Improvement**
- **More Diverse Benchmarks**: While MNIST is a reasonable start, real-world distributed data could be more irregular than a simple Dirichlet partition. Adding more varied datasets (e.g., from large-scale text or image tasks, or from industry-scale streaming data) would broaden the demonstration of the method’s performance.
- **Full Validation of \(\delta\)**: The authors claim that as \(\alpha\) increases, local objectives become more similar (\(\delta\) decreases). However, they do not empirically measure or approximate \(\delta\). A direct empirical validation of \(\delta\)’s role would strengthen the link between method and claimed advantages.
Overall, the proposed methods and evaluation criteria (communication rounds, local gradient steps, final training loss or gradient norm) are coherent for the paper’s decentralized-learning context. While the experimental design could be expanded with more datasets and more direct measurement of data similarity, the chosen metrics and problem setups do largely align with how such methods are tested in the broader decentralized optimization literature.
Theoretical Claims: 1. The paper introduces \delta via
\frac{1}{n} sum_{i=1}^n \|\nabla h_i(x) - \nabla h_i(y)\|^2
\delta^2 \,\|x - y\|^2,
where h_i(x) = f(x) - f_i(x).
This condition implies a “second-order” type similarity across nodes. However, in practical large-scale systems, it often suffices to assume the simpler Lipschitz-smooth condition on each f_i. Your proposed approach places an emphasis on the difference h_i as if each node’s local function is nearly identical to f.
The text does not thoroughly discuss the real-world consequences if \delta is not as small as assumed. In particular, while \delta\leq L always holds when each f_i is L-smooth, the presentation glosses over the implications of \delta being close to L. When \delta\approx L, do the improvements over classical decentralized methods persist or vanish? A deeper quantitative exploration would strengthen the argument.
2. In the “Inexact-PDO” framework, one solves, at each node i:
x_{i}^{(r + 1/2)}
\approx
\arg\min_{x} (
f_i(x)+\;\langle h_i^{(r)},\,x\rangle + \tfrac{\lambda}{2}\|x - x_{i}^{(r)}\|^2
).
This subproblem solution is then subjected to a gradient-norm accuracy requirement, for instance
\sum_{i=1}^n \|\nabla F_{i,r}(x_{i}^{(r + 1/2)})\|^2
\frac{\delta\,(4\,\delta+\mu)}{4(r+1)(r+2)}
\sum_{i=1}^n
\|x_{i}^{(r + 1/2)} - x_i^{(r)}\|^2.
or something of that flavor depending on the theorem.
The paper asserts (e.g., Theorem 1 and subsequent corollaries) that as long as these local subproblems are solved “just enough,” one obtains the same rate as an exact solution. However, it leaves open the question of how many iterations of, say, Nesterov’s or plain gradient descent one actually needs on typical problem instances before the sum of squared gradient norms condition is met. In a typical large neural-net scenario, bounding the subproblem error explicitly would require non-trivial additional assumptions. The paper’s guidelines could be clearer, for example by including bounds on the per-round local iteration cost or enumerating precisely how local complexity scales with \delta \mu, and the network size n.
3. The authors emphasize that the new method “only” needs \mathcal{\tilde O}(\frac{\delta}{\mu(1-\rho)}\log(\frac{1}{\varepsilon}) communications in the strongly convex case, improving from \delta_{\max} to \delta.
At the same time, they do not solve each local subproblem exactly, so the iteration cost is typically \mathcal{\tilde O}(\sqrt{\tfrac{L}{\delta+\mu}}) or something close (depending on the theorem) for each subproblem. Although the paper is correct that \delta < \delta_{\max} may confer a significant advantage if local data are indeed “similar,” it might also be that local subproblems require many gradient steps if \delta is not truly small relative to L. The statements about “lower communication cost” can be somewhat overshadowed if the local computations blow up.
4. While the authors adapt the classic Hybrid Projection Proximal-Point idea (Solodov & Svaiter style) to the decentralized setting, the transitions from \mathbf{x}-updates to \mathbf{v}-updates are presented somewhat abruptly. The role of the stabilizing variable \mathbf{v}, especially in how it prevents the subproblems from requiring ever-increasing precision, is mathematically elegant but might be clearer if placed in a stand-alone lemma that (i) proves stability and (ii) ensures the same or better rate as the simpler approach. Currently, the text interweaves the definitions with the main theorems, and it is easy for the reader to lose track of the key steps that guarantee the claimed \mathcal{\tilde O}(\log(\frac{1}{\varepsilon})) complexity.
Experimental Designs Or Analyses: 1. Nowhere do the authors directly measure or approximate \delta (the second-order dissimilarity measure) in the actual experiments. Instead, they rely on \alpha from the Dirichlet distribution as a surrogate. Mathematically, it would be more rigorous to approximate \delta in practice—for instance by sampling the norms \|\nabla f_i(x)-\nabla f_j(x)\| for random x values—and plotting them, so the audience can see how \delta scales with \alpha. This would confirm that changes in \alpha truly reflect the second-order similarity the theorems rely on.
2. When regularization is small or absent \mu \approx 0, the theoretical bounds predict the “convex case” complexities. However, the experiments do not provide a quantitative link between \mu and the actual speed. In particular, one expects the theoretical number of rounds for a certain \varepsilon-accuracy to be on the order of \mathcal{O}(\tfrac{\delta}{(1-\rho)\varepsilon}) if \mu = 0. Yet the main figures only show *empirical* curves without clarifying whether they align with or deviate from \mathcal{O}(\frac{1}{\varepsilon} or \mathcal{O}(\log(\tfrac{1}{\varepsilon})). It would be helpful to fit the observed convergence data to a model or produce a slope in log–log space, so the experimental results can be interpreted alongside the proposed theorems.
3. It would strengthen the experimental section if the authors demonstrated at least one experiment systematically varying M—for instance, letting M take on \{1, 5, 10, 20\}—so that one can see how error from incomplete averaging impacts performance. For example, if \rho is large (due to a sparse topology), the authors claim we need more gossip steps to maintain \rho^M \le \tfrac{\delta}{6L}. But no chart in the paper explicitly shows how changing M in practice affects communication overhead, final test accuracy, or speed of convergence. This is a missed opportunity to confirm the theory.
4. In the main results, multiple hyperparameters—\(\lambda\), \(M\), local-step learning rate \(\eta\), etc.—are presumably tuned. However, the paper shows only a single set of final curves comparing the proposed method with baselines. It would be more persuasive to include plots (or at least a table) that show how the final performance depends on each hyperparameter. For example, if \(\lambda\) is set too large, do local subproblems become trivial or degenerate, and does that hamper performance? If \(\eta\) in the local subproblem solver is too large, do we see instability? The authors do mention some tuning, but they do not systematically present the experimental process. This makes reproducibility more difficult, and it also leaves open the question of how sensitive the proposed method is to hyperparameters compared to classical gradient tracking or SONATA.
5. The paper’s plots do not show confidence intervals or variance across runs. This is standard practice in many experimental ML contexts to gauge robustness. If the proposed method’s advantage is that it converges faster in both “communication rounds” and “computation steps,” but at the cost of some potential variance from the approximate subproblem solutions, readers should see that tradeoff empirically. For instance, one might observe that fewer gossip steps or fewer local subproblem iterations lead to higher variance in the final solution. The paper could show standard deviation bands or quartiles across multiple random seeds.
Supplementary Material: I read through the main theoretical appendices (labeled as Sections C–F in the supplementary material) where the authors provide detailed proofs of their core theorems (the inexact proximal-point analysis, the stabilized updates, and the accelerated version). That includes:
- The expanded proofs of Theorem 1 (Inexact-PDO) and Theorem 3 (Stabilized-PDO),
- The supporting lemmas on bounding the error from local subproblem solves,
- The proof techniques showing how the gossip averaging errors factor into the overall convergence bounds,
- The analysis for Accelerated-SPDO, including the Monteiro–Svaiter-inspired acceleration steps.
I also looked over the appended numerical details (where they discuss specific parameter choices, such as the Dirichlet parameter \alpha, the choice of \lambda, and how many local iterations are used) to see how the authors aligned their experimental design with their theoretical prescriptions.
Relation To Broader Scientific Literature: 1. The paper fundamentally relies on the classic Proximal-Point Method, originally studied in the single-node, centralized setting. Past work has shown that one can address inexact subproblem solutions via “hybrid” or “projection-based” proximal iterations (Solodov, Mikhail V., and Benar Fux Svaiter. "A new projection method for variational inequality problems." SIAM Journal on Control and Optimization 37.3 (1999): 765-776. Monteiro, Renato DC, and Benar F. Svaiter. "Iteration-complexity of block-decomposition algorithms and the alternating direction method of multipliers." SIAM Journal on Optimization 23.1 (2013): 475-507.). By adapting these ideas to the decentralized environment, this paper continues a line of research on how to relax exact subproblem requirements while still maintaining strong theoretical guarantees.
2. In the decentralized setting, accelerating methods like SONATA or gradient-based approaches often requires delicate handling of local steps or momentum terms. (Tian, Ye, et al. "Acceleration in distributed optimization under similarity." International Conference on Artificial Intelligence and Statistics. PMLR, 2022) for second-order similarity (with \delta_{\max}) but mandated exact or high-precision subproblem solves at each round.
Essential References Not Discussed: NA.
Other Strengths And Weaknesses: 1. While the paper introduces a well-crafted approach, it is also somewhat incremental: it adapts prior tools (e.g. Monteiro–Svaiter acceleration, Gossip averaging, SONATA) rather than introducing a wholly new algorithmic paradigm. The novelty lies chiefly in how these ideas are fused, rather than in an entirely new foundational concept.
2. Although the appendices are extensive, the main body can feel dense at times. Key distinctions—like why the new “stabilized” scheme so dramatically eases local subproblem accuracy demands—could be emphasized more. Some readers may need more immediate intuition or examples within the text (rather than buried in appendices).
3. The methods involve multiple hyperparameters (λ, 𝑀, local step sizes, acceleration constants). The paper gives guidelines, but does not comprehensively detail how sensitive the final performance is to these parameters.
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for your constructive comments.
We have addressed the concerns about missing ablation studies and included the results in our rebuttal below. We agree that these additional experiments significantly strengthen our paper. We kindly ask the reviewer to reconsider the evaluation and, if possible, adjust the score to reflect these changes.
> The authors do not measure or estimate $\delta$ (the second-order similarity measure) directly on these data splits [...]
Thank you for your suggestion.
We randomly sampled $100$ points from $\mathcal{N}(0, I / \sqrt{2d})$ and reported the approximation of $\delta$.
The following table indicates that $\delta$ decreases as $\alpha$ increases.
Thus, examining the performance of methods with various $\alpha$ is a proper way to evaluate the effect of $\delta$.
We promise to add this table in the camera-ready version.
| $\alpha$ | $0.01$ | $0.1$ | $1.0$ | $10.0$ |
|---|---|---|---|---|
| Approximation of $\delta$ | $1.6 \times 10^{-2}$ | $9.2 \times 10^{-3}$ | $2.1 \times 10^{-3}$ | $5.0 \times 10^{-4}$ |
> The authors do not show error bars or repeated runs to reveal the variance.
We promise to run our experiments several times and report their variance in the camera-ready version.
> Real distributed environments might have node-level heterogeneity in CPU/GPU power.
We agree with the importance of considering the settings where each node has different computational resources. However, developing algorithms in this simple setting is an important first step for studying algorithms in the more challenging setting, as the reviewer mentioned. We believe that our work provides helpful insights that could contribute to the development of future algorithms for more realistic settings.
> It would strengthen the experimental section if the authors demonstrated at least one experiment systematically varying M—for instance, letting $M$ take on $\{1, 5, 10, 20\}$ [...]
Thank you for the suggestion.
In the following table, we fixed the number of multiple gossip averaging $M$ of SPDO and listed the gradient norm reached after $2000$ communication.
| $M$ | $1$ | $2$ | $3$ | $5$ | $10$ | $20$ |
|---|---|---|---|---|---|---|
| $\| \nabla f (\bar{x}) \|^2$ (SPDO) | $9.13 \times 10^{-5}$ | $8.32 \times 10^{-5}$ | $2.24 \times 10^{-5}$ | $1.01 \times 10^{-5}$ | $8.55 \times 10^{-5}$ | $5.13 \times 10^{-4}$ |
The hyperparameters, except for $M$, were tuned as in Figure 1(a) with $0.01$ L2 regularization.
The table indicates that setting $M$ to $5$ is optimal.
Comparing the results with $M=1, 2, 3, 5$, increasing the number of gossip averaging decreased the gradient norm.
This implies that performing gossip averaging multiple times is important.
Furthermore, increasing the number of gossip averaging too much increases the gradient norm since the total number of communication is fixed (See lines 422-425).
These observations are consistent with Theorem 3.
We promise to add this table to the revised manuscript.
> It would be more persuasive to include plots (or at least a table) that show how the final performance depends on each hyperparameter. [...]
According to the reviewer's suggestion, we examined the sensitivity of $\lambda$.
The following table shows the gradient norm reached after running algorithms for $2000$ communication.
| $\lambda$ | $0.1$ | $1$ | $10$ | $50$ |
|----|---|---|---|---|
| $\| \nabla f (\bar{x})\|^2$ (SPDO) | $1.13 \times 10^{-1}$ | $8.55 \times 10^{-5}$ | $1.69 \times 10^{-2}$ | $2.44 \times 10^{-1}$ |
If we use a very large $\lambda$, the number of iterations of a local solver can decrease (see Lemma 31), while it requires more communication since the parameters are almost the same even after solving the subproblem, which ultimately requires a large number of communications.
We can see consistent observations in the above table.
We will numerically analyze the sensitivity of other hyperparameters and promise to report the results in the revised manuscript.
> When $\delta\approx L$, do the improvements over classical decentralized methods persist or vanish?
In the worst case, such as $\delta \approx L$, Stabilized PDO and Gradient Tracking require the same communication complexities.
However, in many practical scenarios, $\delta$ is smaller than $L$ [2,3].
For instance, many existing papers, e.g., [1], considered that Dirichlet distribution with $\alpha=0.1$ was heterogeneous. Even in this setting, Figure 1 indicates that our proposed methods can achieve lower communication complexities than Gradient Tracking.
We will clarify it in the revised manuscript.
## Reference
[1] Lin et. al., Quasi-global momentum: Accelerating decentralized deep learning on heterogeneous data. In ICML 2021
[2] Chayti et. al., Optimization with Access to Auxiliary Information, In TMLR 2024
[3] Kovalev et. al., Optimal gradient sliding and its application to optimal distributed optimization under similarity.
In NeurIPS 2022.
---
Rebuttal Comment 1.1:
Comment: Thanks for the authors' effort addressing the concerns. The concerns raised up were almost clarified and addressed. I would update my score accordingly.
---
Reply to Comment 1.1.1:
Comment: Thank you for raising your score. Once again, we sincerely appreciate the reviewer’s insightful comments. | Summary: This paper provides a decentralized optimization method for convex optimization under the second-order similarity. The main contribution is improving the term $\delta_{\max}$ or $L$ to $\delta$ in the complexity to $\delta$.
## update after rebuttal
The authors have addressed my questions, and I decided to keep my overall rating.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I have briefly read the proofs and it sounds correct.
Experimental Designs Or Analyses: The comparison on the computational cost should be involved.
Supplementary Material: I have briefly read the proofs and it sounds correct.
Relation To Broader Scientific Literature: See questions.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: See questions.
Other Comments Or Suggestions: See questions.
Questions For Authors: This paper is well-written and well-motivated. I have briefly sketched the proof, which sounds correct. There are some comments:
1. The main idea seems be to directly combine the inexact gradient sliding (Kovalev et al., 2022) with Multiple Gossip and gradient tracking. Can you highlight the main technical novelty in the algorithm and analysis?
2. The domains of $\bf x$ and $\bf v$ in lines 4-5 of Algorithm 3 and lines 12-13 in Algorithm 4 should be presented.
3. The experimental results only includes the comparison on the communication cost. I think the comparison on the computational cost is also required.
4. Although the main theorems improve the previous ones, the further discussion for the potentially better results is desired:
a) Can we avoid the term $1/\sqrt{1-\rho}$ in the computational cost?
b) Can we introduce the partial participate framework to reduce the complexity of local first-order oracle?
c) Can we provide the lower bound the verify the optimality of proposed algorithms?
The following references may be helpful to the discussion:
[1] Haishan Ye, Luo Luo, Ziang Zhou, and Tong Zhang. Multi-consensus decentralized accelerated gradient descent. Journal of machine learning research 24(306):1-50, 2023.
[2] Qihao Zhou, Haishan Ye, and Luo Luo. Near-Optimal Distributed Minimax Optimization under the Second-Order Similarity. In Advances in Neural Information Processing Systems, 2024.
[3] Aleksandr Beznosikov, Gesualdo Scutari, Alexander Rogozin, and Alexander Gasnikov. Distributed saddle-point problems under data similarity. In Advances in Neural Information Processing Systems, 2021.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive feedback and careful review.
> The main idea seems be to directly combine the inexact gradient sliding (Kovalev et al., 2022) with Multiple Gossip and gradient tracking. Can you highlight the main technical novelty in the algorithm and analysis?
We would like to emphasize that **a straightforward combination of gradient sliding, multiple gossip averaging, and gradient tracking does not work**. To overcome this, we proposed a carefully designed modification in Algorithm 3 (see the update rule highlighted in blue).
Specifically, straightforwardly combining them yields the update rules shown in lines 263-274. However, as we described in lines 275-289, this simple combination does not work.
Our paper is the first to analyze this challenge and develop a principled modification that ensures low communication and computational complexities.
> The domains of $x$ and $v$ in lines 4-5 of Algorithm 3 and lines 12-13 in Algorithm 4 should be presented.
The domains of $x$ and $v$ are $\mathbb{R}^d$. We will clarify them in the camera-ready version.
> The experimental results only includes the comparison on the communication cost. I think the comparison on the computational cost is also required.
The comparison of the computational costs is shown in the second and fourth figures in Figure 1.
The first and third figures from the left show the communication complexities.
We will clarify it in the revised manuscript.
> Can we avoid the term $1/\sqrt{1-\rho}$ in the computational cost?
We deeply appreciate the reviewer for checking it carefully.
There are typos in Table 1; the computational costs for methods other than Gradient Tracking do not depend on $\rho$ since $\tfrac{1}{\sqrt{1 - \rho}}$ in communication complexity comes from the multiple gossip averaging, which does not affect the total computational complexity.
The statements of our theorems in the paper are correct, and this correction does not affect the discussion in the entire paper.
We apologize for your confusion.
We promise to replace Table 1 with the following version in the revised manuscript.
| Method | # Computation |
|--------------------------------|---------------------------------------------|
| Gradient Tracking | $\tilde{\mathcal{O}} (\frac{L}{\mu (1 - \rho)^2} \log (\frac{1}{\epsilon}))$ |
| Exact-PDO (SONATA) | n.a. |
| Inexact-PDO | $\tilde{\mathcal{O}} (\frac{\sqrt{\delta L}}{\mu} \log (\frac{1}{\epsilon}) \log \log (\frac{1}{\epsilon}))$ |
| Stabilized-PDO | $\tilde{\mathcal{O}} (\frac{\sqrt{\delta L}}{\mu} \log (\frac{1}{\epsilon}))$ |
| Accelerated SONATA | n.a. |
| Inexact Accelerated SONATA | $\tilde{\mathcal{O}} (\frac{\sqrt{\delta L}}{\mu} \log (\frac{1}{\epsilon})^2)$ |
| Accelerated Stabilized-PDO | $\tilde{\mathcal{O}} (\sqrt{\frac{L}{\mu}} \log (\frac{1}{\epsilon}))$ |
> Can we provide the lower bound the verify the optimality of proposed algorithms?
Thank you for the comments. We will add the following discussion in the camera-ready version.
**Communication Complexity:**
[1] showed that lower bound requires at least
\begin{align*}
\Omega \left( \sqrt{\frac{\delta}{\mu (1 - \rho)}} \log \left( \frac{\mu \| x^\star \|^2}{\epsilon} \right) \right)
\end{align*}
communication to achieve $f (x) - f (x^\star) \leq \epsilon$.
Our Accelerated SPDO can achieve the following communication complexity:
\begin{align*}
\tilde{\mathcal{O}} \left( \sqrt{\frac{1 + \frac{\delta}{\mu}}{1 - \rho}} \log \left( 1 + \sqrt{\frac{\min \\{ \mu, \delta\\} \|x^{(0)} - x^\star \|^2}{\epsilon}} \right) \right)
\end{align*}
Thus, when $\delta \geq \mu$, Accelerated SPDO is optimal up to the logarithmic factor.
**Computational Complexity:**
For non-distributed cases, any first-order algorithms requires at least
\begin{align*}
\Omega \left( \sqrt{\frac{L}{\mu}} \log \left(\frac{\mu \| x^{(0)} - x^\star \|^2}{\epsilon} \right) \right)
\end{align*}
gradient-oracles to satisfy $f(x) - f^\star \leq \epsilon$ (See Theorem 2.1.13 in [2]).
Accelerated SPDO can achieve the following computational complexity:
\begin{align*}
\tilde{\mathcal{O}} \left( \sqrt{\frac{L}{\mu}} \log \left( 1 + \sqrt{\frac{\min \\{ \mu, \delta\\} \|x^{(0)} - x^\star \|^2}{\epsilon}} \right) \right)
\end{align*}
Thus, the computational complexity of Accelerated SPDO is optimal up to logarithmic factors.
## Reference
[1] Tian, Y., Scutari, G., Cao, T., and Gasnikov, A. Acceleration in distributed optimization under similarity. In AISTATS, 2022.
[2] Nesterov, Y. Lectures on convex optimization. In Springer, 2018.
---
Rebuttal Comment 1.1:
Comment: Thanks for your careful response. I have no further question and decide to keep my rating.
---
Reply to Comment 1.1.1:
Comment: Thank you for your valuable feedback. | null | null | null | null | null | null |
CLIMB: Data Foundations for Large Scale Multimodal Clinical Foundation Models | Accept (poster) | Summary: This paper introduces the Clinical Large-scale Integrative Multi-modal Benchmark (CLIMB), a benchmark unifying diverse clinical data across imaging, language, temporal, and graph modalities. The dataset comprises 4.51 million patients distributed across multiple modalities. The authors conduct extensive empirical evaluations and demonstrate three key findings: (1) Multitask pretraining significantly improves performance on understudied domains. (2) Models pretrained on CLIMB demonstrate improved few-shot transfer learning capabilities, and (3) Unimodal encoder performance translates well to multimodal tasks when paired with appropriate fusion strategies.
Claims And Evidence: Generally, the claims made in this submission are well-supported.
1. Multitask pretraining improving performance on understudied domains: the authors provide evidence in Figure 4, showing substantial AUC improvements for understudied modalities.
2. The second claim regarding few-shot transfer is supported by experiments in Figure 7, demonstrating improvements across various modalities including ultrasound, CT, and ECG domains when using CLIMB pretraining versus standard pertaining.
3. The third claim about fusion strategies is supported by results in Table 5, showing that different fusion methods (late fusion, MLP, cross-attention) exhibit varying effectiveness depending on the task complexity.
However,
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are well-suited for the problem.
Theoretical Claims: The paper does not contain formal proofs for theoretical claims.
Experimental Designs Or Analyses: I reviewed the experimental designs and analyses in detail and found them to be generally sound. The authors use appropriate statistical measures and the multitask training setup is well-designed.
Supplementary Material: I reviewed the supplementary material related to the detailed data descriptions and model performances.
Relation To Broader Scientific Literature: The paper positions itself well within the broader scientific literature on clinical AI and multimodal learning. The authors compare CLIMB to existing medical benchmarks like BenchMD, PMC-VQA, GMAI-MMBench, and CARES.
Essential References Not Discussed: A few references that should be included like recent work on multimodal foundation models in healthcare like BiomedCLIP published in NEJM AI (https://ai.nejm.org/doi/full/10.1056/AIoa2400640), and works on self-supervised learning for medical imaging.
Other Strengths And Weaknesses: **Strengths**
1. The scale and diversity of the CLIMB benchmark is impressive.
2. The focus on understudied modalities and underrepresented regions is valuable for addressing biases in clinical AI.
**Weaknesses**
1. The paper focuses on supervised multitask pretraining rather than exploring self-supervised approaches, which might be more data-efficient and better leverage the unlabeled portions of clinical data, also no bias problem.
2. The improvement in understudied domains might be primarily attributable to increased data exposure rather than true cross-task knowledge transfer.
Other Comments Or Suggestions: 1. The authors should discuss why multitask pre-training instead of self-supervised methods (like masked image modeling or contrastive learning), which might better leverage the large-scale nature of CLIMB.
2. A more thorough analysis separating the effects of increased data quantity from the benefits of multitask learning would strengthen the paper. For example, comparing with models trained on equivalent amounts of data but without task sharing.
3. The paper would benefit from a more detailed analysis of when multitask learning helps versus when it potentially causes negative transfer, as Figure 4 shows varying impacts across datasets.
Questions For Authors: 1. Have you explored self-supervised pretraining approaches as an alternative to supervised multitask learning?
2. To what extent are the improvements in understudied domains attributable to multitask learning specifically versus simply having access to more training data? Have you conducted ablation studies with equivalent data quantities in single-task settings?
3. Figure 4 shows that some datasets experience minimal gains or even slight performance decreases with multitask pretraining. What factors determine whether dataset benefits from multitask learning, and could you elaborate on potential cases of negative transfer?
4. How did you address potential biases in the datasets, particularly for underrepresented regions?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: W1-2, Q1-2, C1-2: In our previous experiments, both pretraining and multitask learning are performed in Exp. 1. We added experiments below comparing unsupervised pretraining vs supervised multitask learning.
First, we found time series models benefited substantially from unsupervised pretraining. As illustrated in App. Tab. 26, we conducted unsupervised masked autoencoder (MAE) pretraining and compared it with pretraining on target dataset only:
| Model | PT Dataset | Eval. Dataset | AUC | Sens. | Spec. |
| --- | --- | --- | --- | --- | --- |
| ECG-JEPA | PTB-XL | PTB-XL | .868 | .195 | .979 |
| ECG-JEPA | CLIMB | PTB-XL | .895 | .210 | .980 |
We found pretraining on diverse data effectively improved the downstream outcome on the target dataset. Similarly, for EEG datasets, as shown in App. Table 24, pretraining on a diverse range of data improved the performance for 2/3 datasets and overall:
| Model Name | IIIC | | | | TUEV | | | | TUAB | | | | Overall | | | |
|------------|------|------|------|------|------|------|------|------|------|------|------|------|------|------|------|------|
| | AUC | Sens | Spe | F1 | AUC | Sens | Spe | F1 | AUC | Sens | Spe | F1 | AUC | Sens | Spe | F1 |
| Single Task | .854 | .510 | .905 | .499 | .856 | .466 | .908 | .371 | **.879** | **.798** | **.798** | **.799** | .863 | .591 | .870 | .556 |
| MTL Only | .848 | .484 | .901 | .475 | .903 | .386 | .932 | .387 | .844 | .764 | .764 | .761 | .865 | .545 | .866 | .541 |
| Pretrain+MTL | **.862** | **.546** | **.911** | **.531** | **.878** | **.549** | **.917** | **.397** | .869 | .794 | .794 | .795 | **.870** | **.630** | **.874** | **.574** |
While combining pretrain and multitask learning achieves the best results, pretraining seems to play a larger role than multitask learning in EEG models.
On the other hand, we showed in Fig. 4 that multitask learning effectively improved the vision encoder’s performance. Surprisingly, vision models did not benefit from further pretraining, and only multitask learning helps:
| PT Method | Model | CXR | | | Mammo | | | Derm | | | CT | | | Fundus | | | US | | | Overall | | |
|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
| | | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe |
| MAE + MTL on CLIMB | ConvNeXTv2 | 0.801 | 0.379 | 0.923 | 0.489 | 0.276 | 0.671 | 0.795 | 0.414 | 0.738 | **0.699** | 0.430 | 0.614 | 0.757 | 0.325 | 0.835 | 0.705 | 0.484 | 0.687 | 0.733 | 0.433 | 0.766 |
| MAE + CL + MTL on CLIMB | InternViT | 0.753 | 0.338 | 0.906 | 0.500 | 0.287 | 0.689 | 0.767 | 0.353 | 0.715 | 0.678 | 0.409 | 0.595 | 0.683 | 0.298 | 0.825 | 0.683 | 0.532 | 0.689 | 0.697 | 0.394 | 0.743 |
| **Only MTL on CLIMB** | ConvNeXTv2 | **0.817** | **0.436** | **0.939** | **0.558** | **0.330** | **0.706** | **0.901** | **0.568** | **0.777** | 0.671 | **0.466** | **0.641** | **0.873** | **0.563** | **0.888** | **0.774** | **0.641** | **0.770** | **0.787** | **0.537** | **0.806** |
Here, MAE = Masked Autoencoder, CL = Contrastive Learning and MTL = Multitask Learning. For MAE, we followed the same approach as in [ConvNeXTv2](https://arxiv.org/pdf/2301.00808). For contrastive learning, we followed the CLIP-style approach as outlined in [InternVL](https://arxiv.org/abs/2312.14238). In the above vision experiment, neither MAE nor CL pretraining improved the model’s performance for downstream tasks. One hypothesis is that these models are already heavily pre-trained on massive unlabeled natural image corpora, so an additional masked image or contrastive-style phase on clinical data doesn’t substantially shift or enrich their learned representation. We welcome the community’s contribution to better leveraging the diverse labeled data available in CLIMB.
Q3, C3: We found that datasets with novel tasks, Understudied modalities or from Underrepresented regions, as defined in Lines 1219-1290, benefit the most from multitask learning. We believe this is due to the scarcity of data in these categories, which makes data from other modalities or tasks, albeit not closely related, beneficial. On the other hand, if a dataset has a large number of samples or fairly saturated performance on a specialized diagnostic task, then multitask learning may not add much beyond what single-task training already learns.
Q4: During the construction of CLIMB, we aim to include as many datasets from underrepresented regions as possible. This includes datasets from geographically underrepresented regions, as well as data from developing countries where the data has been historically scarce, as defined in Lines 1274-1290. We included a list of dataset collection locations in the App. Table 8. In summary, 8 out of 30 (26.7%) of the datasets with known source locations come from underrepresented regions, a percentage significantly higher than all datasets available from public sources. | Summary: This paper introduces a large-scale clinical multimodal benchmark. The authors conduct multitask pretraining, few-shot transfer, and multimodal fusion. Based on the constructed data, they provide extensive experiment results to answer the proposed research questions.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: There are no proofs or theoretical claims.
Experimental Designs Or Analyses: Yes
Supplementary Material: There is no supplementary material. They provided the appendix.
Relation To Broader Scientific Literature: This work provides contribution to the medical and healthcare domain.
Essential References Not Discussed: They cover most of the recent works. But lack some of them, such as Wang, Xiaochen, et al. "Unity in diversity: Collaborative pre-training across multimodal medical sources." Proceedings of the 62nd Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers). 2024.
Other Strengths And Weaknesses: Strengths:
1, This is a comprehensive multimodal clinical benchmark covering different modalities.
2, This paper introduces the data construction, experiment, evaluation, and discussion.
3, The writing is easy to follow.
Weakness:
1, Figure 3.a and 3.b seem not that clear to understand.
2, I am wondering what computation resources do the users need to implement this approach.
Other Comments Or Suggestions: No
Questions For Authors: Please see the weakness.
Also, is all the data used in this work public? Are the data collection and cleaning scripts provided?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your feedback regarding Figures 3.a and 3.b. Both figures illustrate two different experiments we conducted on CLIMB: multitask learning and transfer learning. The figures display example data from CLIMB (such as x-rays, CT scans, etc.) as inputs to the model and display evaluation on the right. For Figure 3.a, we train a single model on multiple clinical tasks across different medical modalities and evaluate it on each individual dataset. The goal is to evaluate whether a multitask pre-train model can generalize across diverse tasks, including understudied ones. This setup helps assess if shared representations from CLIMB improve generalization within each dataset. In Figure 3.b, a multitask pre-trained model is applied to a new task with limited data to see whether the model adapts its learned representations to the new task, despite having few samples available. The goal is to determine if exposure to a broader range of tasks in CLIMB helps compensate for data scarcity in specific datasets.
To improve clarity, we will implement the following revisions: 1) provide a more detailed figure description 2) move labels for "understudied" and “few samples" to the side to avoid implying they apply to the entire column. We will also cite the recent works mentioned in the review.
Regarding the computational resources, as described in Appendix C.4.2, all experiments are performed on a server with 8xH200 GPUs for the best performance. At least 20TB of storage is needed if you would like to train a model on the entire dataset. With that said, our model is small enough to fit on one GPU with 24GB of VRAM, and the entire training on one GPU would take less than a week.
All data used in this work is public and can be accessed easily using our framework, as outlined in our response to Reviewer pTYB. In summary, a user only needs to complete one-time registrations of two accounts and complete one CITI training, which takes less than 4 hours. Our framework will then prompt the user to agree to agreements, and downloading each dataset will take less than 10 seconds of human labor. Our framework will also handle the data cleaning, processing and standardization of formats. | Summary: This paper introduces the Clinical Large-scale Integrative Multimodal Benchmark (CLIMB), which integrates diverse clinical data across imaging, language, time-series, and graph modalities. CLIMB consists of 4.51 million patient samples (19.01 terabytes), covering 2D imaging, 3D video, and multimodal data. Empirical evaluations demonstrate that multitask pretraining significantly enhances performance, with improvements of 29% in ultrasound analysis and 23% in ECG analysis over single-task learning. Additionally, pretraining on CLIMB improves generalization to new tasks, while strong unimodal encoders effectively contribute to multimodal models when combined with appropriate fusion strategies.
**update after rebuttal**
In my initial review, I had some concerns about the novelty of the proposed unified framework, and the results appeared fairly predictable.
In their response, the authors provided additional clarification on the taxonomy standardization, which I found helpful. Moreover, the improved performance on underrepresented regions and modalities (ultrasound, CT, EEG) is particularly meaningful in the healthcare domain.
Therefore, I am increasing my initial score to 3, leaning toward acceptance.
Claims And Evidence: The primary contribution of this work is the standardization of multiple publicly available datasets to demonstrate that pretraining on a large-scale medical dataset enhances downstream task performance. However, the results appear somewhat predictable, as prior research has already established that large-scale pretraining generally improves model performance.
Methods And Evaluation Criteria: This paper does not propose a novel method, so evaluating a specific methodology is not applicable. However, in terms of evaluation criteria, this work makes contributions by introducing a unified framework for holistic training and benchmarking of clinical models through standardization of data loading and prediction tasks.
The key contributions include:
**Standardized Task Formulation**
- All tasks are framed as multi-label classification across different clinical modalities.
- Terminology variations are standardized, and similar concepts (e.g., Lung Opacity from CheXpert and Infiltration from VinDR-CXR) are merged to create a consistent and clinically meaningful vocabulary.
**Question-Answering (QA) Reformulation**
The dataset is also structured as a closed-choice question-answering (QA) task, named CLIMB-QA, to support comparative evaluation of large vision-language models (LVLMs).
**Unified Data Processing Interface**
- A standardized pipeline is provided for downloading and processing datasets into a unified format, ensuring compatibility for large-scale mixed-modality pretraining (subject to dataset-specific consent agreements).
Beyond the significance and novelty of these contributions, the rationale behind formulating multiple heterogeneous tasks in a unified manner is well-grounded and conceptually sound.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experiments are designed to address the following three research questions:
Q1: Can multitask-pretrained clinical models perform consistently across multiple tasks, particularly for understudied tasks?
Q2: How well do multitask-pretrained clinical models transfer to new tasks within the same clinical modality, especially when data is limited?
Q3: Can multitask-pretrained unimodal models be effectively fused to tackle multimodal clinical tasks?
If the novelty and significance of these research questions are set aside, the experiments themselves are adequately designed to address them. However, regarding the first and third questions, the conclusion is fairly predictable—multitask learning tends to be particularly beneficial in scenarios where data or research focus has historically been limited.
For the second question, the paper concludes that the large-scale pretraining dataset enables efficient learning of novel tasks with limited samples, yielding consistent performance improvements across all modalities. While this finding aligns with the results presented, it largely re-claims well-established principles in machine learning.
Supplementary Material: I’ve read the following parts: Appendix A, Table 7 and 28.
Relation To Broader Scientific Literature: It’s related to ML4H.
Essential References Not Discussed: Regarding the primary research questions addressed with CLIMB, I believe that similar findings have already been demonstrated in prior work. Specifically, previous studies have shown that training a foundation model on large-scale medical datasets improves downstream task performance. The following papers provide strong evidence in support of this claim:
- Med Gemini (arXiv:2405.03162)
- BiomedGPT (arXiv:2305.17100)
- RadFM (arXiv:2308.02463)
I assume that the authors are already well aware of these works. Given this, a clearer differentiation of CLIMB’s unique contributions—beyond reaffirming known benefits of large-scale pretraining—would further strengthen the impact of this study.
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: **Comment on Figure 4**
The authors define underrepresented regions and understudied modalities. For underrepresented regions, Brazil and China are mentioned. Could you clarify why these countries are considered underrepresented in the medical domain? Do the individual datasets listed in Table 6 lack sufficient samples from Asian and South American cohorts? Providing statistical evidence would make this argument more convincing.
Regarding understudied modalities, ultrasound and CT scans are included. However, this characterization may be somewhat misleading, as both modalities play a crucial role in daily clinical practice. I believe the authors intended to highlight the relative scarcity of publicly available datasets for these modalities compared to others. It would be helpful to clarify this point more explicitly.
**Comment on dataset construction**
I am particularly interested in how similar medical concepts are merged or how terminology is standardized, as this is a crucial preprocessing step when handling large-scale medical data for model training.
For chest X-ray datasets, did you merge lung opacity and infiltration into a single category, such as lung opacity? If so, could you provide the final list of combined classes used in the dataset?
Additionally, VinDR defines diseases (e.g., pneumonia, cancer, tuberculosis) based on findings such as nodules, fibrosis, consolidations, and etc. How did you establish the mapping between diseases and their corresponding findings? Understanding the rationale behind these classifications would provide better insight into the dataset's structure and its impact on model performance.
**Suggestion**
Combining and refining publicly available datasets is valuable and provides significant benefits to the research community. However, in my opinion, a more substantial revision of the dataset should be undertaken. For example, the relabeled version of ImageNet (Beyer et al., 2020) has been widely appreciated for improving data quality. Similarly, in image-text datasets, re-captioning existing datasets such as LAION or Conceptual Captions (CC) has proven helpful for researchers and practitioners.
Following this direction, this work would greatly benefit from further efforts to refine the existing datasets. One possible approach is to standardize terminology more rigorously in collaboration with domain experts, such as thoracic radiologists. Although this work has made some efforts toward standardization, I could not find detailed information on the extent of these efforts. Specifically, it remains unclear how many radiologists were involved and what process was followed for standardization. Additionally, rephrasing existing Chest X-ray reports using standardized medical terminology would be highly valuable for deep learning applications in radiology. These enhancements would improve the dataset’s usability and reliability, ultimately benefiting clinical AI research.
Questions For Authors: Please refer to the comment section above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate reviewer SVNB's feedback. Besides our scale and focus on multimodal, our work distinguishes itself from related research in several ways:
- Our focus extends beyond confirming general pretraining benefits by specifically targeting underrepresented regions and modalities (ultrasound, CT, EEG). These more rare, OOD tasks have demonstrated superior performance gain as compared to tasks that occur often in the datasets. This challenges the traditional idea that pretraining mainly helps with popular tasks while struggling to improve perf. on OOD tasks (https://arxiv.org/abs/2211.08411, https://arxiv.org/abs/2212.10511).
- In addition, we show that traditional vision encoders still perform better than medical VLLMs by a large margin, whereas related works mentioned in the review mainly focus on improving VLLMs.
- We release a unified framework that streamlines downloading, processing, and model training across vision, time series, and graph domains, enabling researchers to rapidly replicate and iterate on methods against diverse clinical tasks. Our work is of a much larger scale than related works, as shown in our response to Reviewer pTYB.
Comment on Figure 4: We define underrepresented regions and understudied modalities in Lines 1219-1290 using a two-step approach that identified geographic and economic gaps in dataset coverage. While 8/30 (26.7%) datasets with known collection sites come from these regions, this representation still lags behind developed countries. We will clarify that our classification of understudied modalities reflects public dataset availability rather than clinical importance.
On dataset construction: We put extensive efforts into standardizing the taxonomy. Standardization is difficult as it requires balancing two competing objectives:
- Merging similar terms to facilitate learning and cross-modality transfer
- Minimizing information loss and avoiding inaccuracies when modifying labels
Our standardization efforts concentrated on ECG and chest X-ray, which offer fine-grained labels with varying terminologies. For ECG, we followed approaches from [arXiv:2304.08486](https://arxiv.org/abs/2304.08486) and formulated a mapping [here](https://anonymous.4open.science/r/climb_submission-5D0E/Label_Processing.md) in our anonymous repo.
For Chest X-rays, we developed a new mapping with radiologist input. Following practices from [1](https://pmc.ncbi.nlm.nih.gov/articles/PMC10173935), [2](https://www.nature.com/articles/s41598-023-33303-y) and [3](https://pmc.ncbi.nlm.nih.gov/articles/PMC11455863/), we consolidated all Chest X-ray labels into the CheXpert 14 categories:
| Raw Label | Standardized Label |
|-----------|-------------------|
| Aortic enlargement, Enlarged PA | Enlarged Cardiomediastinum |
| Cardiomegaly | Cardiomegaly |
| Atelectasis | Atelectasis |
| Consolidation | Consolidation |
| Edema | Edema |
| Infiltration, Lung Opacity, ILD, Pulmonary fibrosis | Lung Opacity |
| Nodule/Mass, Other lesion, Lung cavity, Lung cyst, Lung tumor | Lung Lesion |
| Pleural effusion | Pleural Effusion |
| Pleural thickening | Pleural Other |
| Pneumothorax | Pneumothorax |
| Rib fracture, Clavicle fracture | Fracture |
| No finding | No Finding |
| Support Devices | Support Devices |
| Pneumonia | Pneumonia |
Labels from other modalities with the same name are then merged with these classes. We acknowledge standardization may affect label granularity, particularly for lung opacity and lung lesion classes. CLIMB provides both standard and raw labels, allowing researchers to prioritize either granularity or standardization. All experiments in our work used standard labels.
To evaluate standardization effects, we compared vision encoders trained on raw versus standardized labels:
| Model | CXR | | | Mammo | | | Derm | | | CT | | | Fundus | | | US | | | Overall | | |
|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
| | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe | AUC | Sen | Spe |
| ConvNextV2-RawLabel | **.820** | .358 | .935 | .543 | .293 | .693 | .853 | .492 | .757 | **.690** | .442 | .624 | .794 | .351 | .841 | .689 | .519 | .713 | .751 | .434 | .766 |
| ConvNextV2-StandardLabel | .817 | **.436** | **.939** | **.558** | **.330** | **.706** | **.901** | **.568** | **.777** | .671 | **.466** | **.641** | **.873** | **.563** | **.888** | **.774** | **.641** | **.770** | **.787** | **.537** | **.806** |
Standardized labels yielded better performance: 3.6% improvement in overall AUC, 10.3% in sensitivity, and 4.0% in specificity. Notably, standardization benefited other modalities more than Chest X-ray itself, where most relabeling occurred. We believe standardized labels help the model connect concepts across modalities more effectively. We hope this work motivates further efforts in terminology standardization and fine-grained relabeling of public clinical datasets. | Summary: The paper introduces CLIMB (Clinical Large-scale Integrative Multimodal Benchmark), a clinical benchmark that puts together a large number of existing datasets across different modalities with a strong focus on vision, including 1D, 2D, and 3D signals, as well as graph data. The authors conduct a thorough comparison of models trained on CLIMB improve performance across a number of different tasks compared to the best existing models in the literature for these tasks (often either pretrained within a single modality). CLIMB is very large scale (including over 4.5M patients and 19TB of data). To obtain CLIMB, one must go through the steps necessary for each individual dataset.
## Update after rebuttal
I have read the rebuttal and will keep my recommendation as is.
Claims And Evidence: - Lines 237-239 (column 2): "To evaluate few-shot generalization, we test on out-of-distribution (OOD) datasets $D_\text{ood} \not\subset D_\text{train}$." => You are claiming that if a dataset is not part of the training datasets used, it is out-of-distribution, but that may not always be the case. Authors themselves explain in lines 185-188 (column 2) that they "balance the dataset such that each modality contains 3-5 datasets, providing multiple data sources per modality while maintaining diversity within each category." It is likely that another dataset will still have a lot in common with the training datasets. Please do not use OOD to describe these datasets unless you formally quantify their "OOD-ness", e.g., by training a membership model.
- In Table 5, you show results for the "SoTA" encoder compared to "Ours". Please include the citation of the paper(s) that introduce the SoTA encoder(s) instead of only "SoTA". Where can we find these papers with SoTA results for LOS and IHM?
- In your impact statement, lines 470-473, you state: "Our holistic evaluation metrics will also encourage the research community to quantify the tradeoffs between performance, complexity, robustness, fairness, and privacy in clinical AI." => I only see evaluation metrics related to standard model performance, and even in that case only simple metrics like AUC, accuracy, precision, and recall are used for classification, and MAE for regression. Please remove that from your impact statement.
Methods And Evaluation Criteria: - Not sure where to mention this, but in my opinion an issue with CLIMB is not explicitly discussing how the user can obtain the data upfront. Anyone working with applications in healthcare know this is a major bottleneck. There are details in the github repository shared and in the appendices about the licences, but it would be nice to have a paragraph early on in the main paper where authors clearly state that users need to obtain approval to access specific datasets, that upon doing that they can use their codebase to download all datasets automatically, that it can take "X" weeks/months to obtain approval, etc.
- One part of the data I find the authors did not explore well (even in the appendices) is textual and EHR data. In fact, CLIMB is mostly an image-first benchmark, perhaps also a time-series-second benchmark. However, there is very little textual or EHR data in CLIMB, but this is not at all something clear from the paper. (For example, in Table 1 "Comparison of clinical benchmarks" it seems that CLIMB "fully covers" the text modality, which I find does not fully tell the truth.) Free-text clinical notes and EHR data are, to the best of my knowledge, only available from MIMIC-IV (one of the numerous datasets used in CLIMB). Even in Appendix A.2, where the "Understudied modalities" are discussed, only images are mentioned. These downsides, such as limited EHR/text data, should be more clearly highlighted to the reader in the main paper. => I am not sure what would be the alternative to showcase this more clearly, but perhaps you could have a plot like a bar plot or a radar chart, where in each dimension you have proxies to the amount of text in the dataset (e.g., "number of words", "number of documents", "size in GB", etc). That way you could compare CLIMB with existing benchmarks (like PMC-VQA, GMAI-MMBench, CARES) in more detail when it comes to the amount of text available in the benchmarks. For this, you should also include, for example, "comments" in the COVID-BLUE dataset, or any other free-text data available.
- For evaluation of in-hospital mortality in Table 5, you should probably include the F-1 score and the area under the precision-recall curve. (Perhaps in the appendix, if that does not fit the main paper.) I find that the answer to RQ3 is a bit lacking compared to the other 2 RQs, RQ1 and RQ3.
Theoretical Claims: No theoretical claims are made in this paper that I could verify.
Experimental Designs Or Analyses: The experimental design used in the paper is comprehensive. The set of baselines compared against is extensive, and it is really nice to see this large-scale, wide comparison being made. The main research questions looked into in this paper have to do with whether pretraining a model on CLIMB improves downstream performance across tasks, and to what extent do models transfer to unseen datasets.
Supplementary Material: I have reviewed (scanned) the entire supplementary material.
Relation To Broader Scientific Literature: Good comparisons to existing benchmarks (Table 1) to the best of my knowledge.
Essential References Not Discussed: No crucial references missing that I noticed to the best of my knowledge.
Other Strengths And Weaknesses: Strengths worth mentioning:
- Very large scale clinical benchmark
- Extensive experiments showing improvements on downstream tasks
Weaknesses specific to each dimension of the review are discussed in the dimension's section.
Other Comments Or Suggestions: - In line 325, you refer to Table D.1 but it links to Table 25 in Appendix D.1.
- If you are going to focus on precision and recall (like in Tables 2, 3, etc), you should probably also include an F-score. The F-score helps quickly see the trade-off between both quantities (which is of course do-able in with only P and R, but considerably slower).
- In all your Tables, only embolden the overall best-performing results (using bold-face). In Table 2, for instance, you embolden InternViT Mammography Sen (.340), but MedViT obtained .417 Sen. You also say in Table 2's caption that "The best performance of each model in AUC is bolded." However, it is not just the AUC that is emboldened. In Table 5, SoTa MLP for 48 IHM (8-Shots) has recall of .536, whereas the entry that is emboldened is Ours MLP with a recall of 0.295. Please fix these typos/mistakes/inconsistencies throughout the paper.
- Figures and Tables in your paper do not appear in the order they are mentioned in the text. Please fix that.
- You often compare few-shot performance with "full dataset" performance, like for instance in Figure 6 or Table 5. I may have missed that, but in "full dataset" do you mean the model is fine-tuned on the full training data available for the task? If that is the case, please do not use "1 shot", "8 shots", and "full", but for the latter use "full FT" instead (and explain in the figure/table caption that FT means fine-tuning).
Questions For Authors: For MIMIC-IV experiments under RQ3: what exactly are the clinical notes you used (radiology reports, discharge summaries)? For modelling length of stay as a regression task, did you do any normalisation of the stay duration?
Is it fair to say that this is an image-first, time-series second benchmark? For instance, in Appendix C4, for your vision experiments you have 8 baseline models, for your EEG/ECG experiments 8 more models, that cover a number of different architectures and strategies. For text and EHR structured data, you have ClinicalBERT.
You mention you use "EHR data" from MIMIC-IV, but I could not find a clear explanation of what exact variables do you mean by that. What are the variables used in your experiments that you refer to as "EHR data"?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer pTYB for the positive reviews and constructive feedback. We have addressed all typographical errors in our manuscript.
Regarding the definition of OOD datasets (Claim 1), we selected OOD datasets primarily based on task differences and provided a comprehensive list with justifications in the App. Table 9. Of the 10 OOD datasets, 7 (COVID-19, CoronaHack, ISIC-2020, BCSS, BUSI, LNDb, PTB-XL-Finegrained) have zero label overlap with other datasets in the same clinical domain, while the remainder feature distinct task granularity. To quantify this heterogeneity, we conducted a membership experiment using ConvNeXT-v2-base as the backbone to predict dataset membership, following hyperparameter settings in Appendix C.4.2. Results confirm our designated OOD datasets exhibit substantial distinctiveness:
|OOD Dataset|Balanced Accuracy|AUC|F1 Score|
|-----------|----------------|---|--------|
|BCSS|99.8|1.000|0.928|
|CBIS-DDSM|99.9|1.000|0.801|
|CoronaHack|99.7|0.999|0.371|
|COVID-19|53.2|0.953|0.112|
|BUSI|99.9|1.000|0.997|
|Jichi|99.8|0.999|0.758|
|ISIC-2020|99.7|0.999|0.841|
Claim 2: In Table 5, "SoTA encoders" refers to the best pre-trained encoders tested across clinical-specific and general domain models. Specifically, as detailed in Sec. 4.1, we employed ConvNextV2, ECG JEPA, and ClinicalBERT. Our experimental protocol follows [FuseMoE](https://arxiv.org/abs/2402.03226), except we implemented regression without binning for LOS to increase granularity, and utilized AUC, sensitivity and specificity for 48 IHM to maintain consistency throughout the paper. We will incorporate a comprehensive results table for experiment 3 in the appendix.
Claim 3: We will remove lines 470-473 from the impact statement. As typical of impact statements, this referred to potential future work. The dataset samples contain demographic information where available, which could facilitate future evaluation of robustness, fairness, and privacy in clinical AI.
Methods 1: Data accessibility was a key consideration in dataset selection, as outlined on page 23 (Dataset Selection Methodology). We specifically selected datasets that do not require lengthy approval processes. Researchers can access 37 of 44 datasets in CLIMB after completing these steps, requiring less than 4 hours total:
- Register for PhysioNet (15 mins) and Kaggle (10 mins) accounts
- Complete CITI certification training (3 hours)
- Acknowledge dataset agreements (10 seconds each)
Our framework then manages all downloads and processing automatically.
Methods 2: CLIMB integrates all metadata, labels and text reports with each sample. We did an analysis of the number of words, the number of QA pairs and the total size of the dataset. Comparing with other multimodal clinical QA datasets:
| Dataset | Number of Words | Num QA Pairs | Size of Dataset |
|----------------|------------------|----------------|------------------|
| CLIMB-QA | 129.1M | 4.51M | 19.01 TB |
| PMC-VQA | 10.2M | 227K | - |
| GMAI-MMBench | 980K | 26K | 49 GB |
| CARES | 1.74M | 41K | 21.61 GB |
Our dataset exceeds others by at least an order of magnitude in all three metrics.
Methods 3: We have added accuracy and F-1 score to Table 5. We include a subset here due to space limit and will add the full table in Appendix of final manuscript:
| | | LOS | 48 IHM (Full) | | | | | 48 IHM (8-Shots) | | | | |
|---|---|---|---|---|---|---|---|---|---|---|---|---|
| **Enc** | **Fusion** | **MAE** | **AUC** | **Sens** | **Spec** | **Accuracy** | **F1 Score** | **AUC** | **Sens** | **Spec** | **Accuracy** | **F1 Score** |
| SoTA | CrossAtt | 2.77 | 0.786 | 0.628 | 0.814 | 0.792 | 0.416646562 | 0.58 | 0.286 | 0.766 | 0.763 | 0.014860231 |
| Ours | MLP | 2.84 | 0.961 | 0.824 | 0.975 | 0.968 | 0.704789834 | 0.672 | 0.295 | 0.858 | 0.767 | 0.290421866 |
| Ours | CrossAtt | 2.61 | 0.796 | 0.822 | 0.59 | 0.825 | 0.90490467 | 0.57 | 0.294 | 0.753 | 0.728 | 0.105340098 |
Question 2: In this work, our focus is on vision, time series and graphs, where large pretraining efforts are particularly scarce. We focused less on textual modality since multiple textual LLMs trained on diverse medical data already exist, including [ClinicalBERT](https://huggingface.co/medicalai/ClinicalBERT) and [BioMistral](https://huggingface.co/BioMistral/BioMistral-7B).
Question 1,3: The EHR data encompasses all textual data available in MIMIC-IV within 48 hours of admission: vital signs, lab measurements, treatments, medications, and demographics. We excluded data without timestamps (e.g., diagnoses) and omitted discharge summaries and radiology reports. We performed no normalization or binning on LOS regression. The text is JSON-formatted and fed directly into the text model for embedding. | null | null | null | null | null | null |
Stacey: Promoting Stochastic Steepest Descent via Accelerated $\ell_p$-Smooth Nonconvex Optimization | Accept (poster) | Summary: The paper uses different mixed Lp norms to run SGD
Claims And Evidence: The main takeaway is that there are different Lp norms boost performance of optimization for different problems. For CNN's for example they find L2 to work best but for LLMs they find another L3 to work better for example. Unfortunately there are no error bars or standard deviation in tables. Also the learning rates for the baseline Adam is very off for LLMs, its set to 1e-4 where it should really be set to 1e-3 or higher. Also the epsilon for Adam is also off. Setting epsilon to 1e-8 basically makes Adam act as SGD + M. On LLMs the epsilon should be set closer to 1e-17.
Methods And Evaluation Criteria: I believe the baselines were not set correctly.
Theoretical Claims: The paper does a good job of contextualizing their method in modern optimization.
The paper gives some extensions to simpler claims from but good overall.
[1] Guillaume Garrigos, Robert M. Gower, Handbook of Convergence Theorems for (Stochastic) Gradient Methods
[2] Ahmed Khaled, Peter Richtárik, Better Theory for SGD in the Nonconvex World
Experimental Designs Or Analyses: please see other sections.
Supplementary Material: I downloaded the code and ran it on a few benchmarks. I did not see a boost in modded-nanoGPT which is a properly tuned baseline. I also did not see a boost vs Adam in some toy problems like xor https://github.com/lixilinx/psgd_torch/blob/master/rnn_xor_problem_general_purpose_preconditioner.py
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: NA
Other Strengths And Weaknesses: The paper lacks variance bars or standard deviations as well as weakly tuned baselines.
Other Comments Or Suggestions: Fix baselines.
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewer for their comments and suggestions.
>**Error Bar and Standard Deviation**
> No error bars or standard deviation in tables
We ran 3 random seeds to obtain the error bar.
CIFAR:
| **Optimizer** | **Train NLL @50** | **Train NLL @100** | **Train NLL @200** | **Test ACC @50** | **Test ACC @100** | **Test ACC @200** |
|---|:---:|:---:|:---:|:---:|:---:|:---:|
| SGD w/ Momentum | 0.0567 ± 0.0017 | 0.0441 ± 0.0014 | 0.0352 ± 0.0012 | 91.15 ± 0.30 | 92.02 ± 0.24 | 92.76 ± 0.13 |
| Adam | 0.0401 ± 0.0017 | 0.0182 ± 0.0017 | 0.0083 ± 0.0010 | 91.69 ± 0.18 | 92.13 ± 0.16 | 92.66 ± 0.36 |
| AdamW | 0.0590 ± 0.0010 | 0.0278 ± 0.0009 | 0.0195 ± 0.0015 | 90.59 ± 0.37 | 91.47 ± 0.42 | 92.12 ± 0.07 |
| Lion | 0.1006 ± 0.0571 | 0.2226 ± 0.1410 | 0.0245 ± 0.0043 | 89.38 ± 2.02 | 89.19 ± 1.88 | 92.15 ± 0.32 |
| Stacey(p,p) | 0.0423 ± 0.0009 | 0.0118 ± 0.0014 | 0.0021 ± 0.0011 | 91.88 ± 0.21 | 92.79 ± 0.16 | 93.79 ± 0.38 |
| Stacey(p,2) | 0.0614 ± 0.0031 | 0.0131 ± 0.0027 | 0.0014 ± 0.0005 | 90.83 ± 0.32 | 92.70 ± 0.28 | 93.54 ± 0.06 |
ImageNet:
| **Optimizer** | **Train NLL @20** | **Train NLL @40** | **Train NLL @60** | **Test Top-1 ACC @20** | **Test Top-1 ACC @40** | **Test Top-1 ACC @60** |
|---|:---:|:---:|:---:|:---:|:---:|:---:|
| Stacey(p,p) | 1.4680 ± 0.0150 | 1.1636 ± 0.0159 | 1.0324 ± 0.0100 | 66.93 ± 0.10 | 69.15 ± 0.15 | 69.87 ± 0.14 |
LLM:
| **Optimizer** | **Train loss @5K** | **Train loss @10K** | **Train loss @20K** | **Train loss @30K** | **Test loss @5K** | **Test loss @10K** | **Test loss @20K** | **Test loss @30K** |
|---|:---:|:---:|:---:|:---:|:---:|:---:|:---:|:---:|
| SGD w/ Momentum | 6.6704 ± 0.0129 | 6.5205 ± 0.0088 | 6.4206 ± 0.0055 | 6.3920 ± 0.0048 | 6.6558 ± 0.0131 | 6.5150 ± 0.0085 | 6.4173 ± 0.0038 | 6.3909 ± 0.0038 |
| Adam | 6.4548 ± 0.0028 | 6.3647 ± 0.0037 | 6.2851 ± 0.0030 | 6.2485 ± 0.0028 | 6.4493 ± 0.0017 | 6.3646 ± 0.0035 | 6.2820 ± 0.0037 | 6.2480 ± 0.0028 |
| AdamW | 5.6655 ± 0.0095 | 5.5172 ± 0.0081 | 5.4401 ± 0.0091 | 5.4268 ± 0.0096 | 5.6510 ± 0.0099 | 5.5171 ± 0.0080 | 5.4350 ± 0.0088 | 5.4240 ± 0.0093 |
| Lion | 6.8722 ± 0.0656 | 6.8190 ± 0.0549 | 6.8021 ± 0.0451 | 6.7794 ± 0.0425 | 6.8624 ± 0.0587 | 6.8220 ± 0.0500 | 6.7954 ± 0.0438 | 6.7733 ± 0.0413 |
| Stacey(p,p) | 5.4016 ± 0.0107 | 4.9938 ± 0.0209 | 4.6492 ± 0.0112 | 4.4962 ± 0.0123 | 5.3616 ± 0.0068 | 4.9655 ± 0.0169 | 4.6372 ± 0.0116 | 4.4879 ± 0.0132 |
| Stacey(p,2) | 6.2492 ± 0.0060 | 6.0038 ± 0.0319 | 5.7210 ± 0.0363 | 5.5841 ± 0.0379 | 6.2312 ± 0.0065 | 5.9867 ± 0.0313 | 5.7062 ± 0.0375 | 5.5755 ± 0.0375 |
>**Baseline Settings**
> Learning rates for the baseline Adam is very off for LLMs; its set to 1e-4 where it should really be set to 1e-3 or higher. Also, the epsilon for Adam is also off. Setting epsilon to 1e-8 basically makes Adam act as SGD + M. On LLMs the epsilon should be set closer to 1e-17.
We would kindly ask the reviewer to provide additional details regarding which LLMs they are referring to, as we did not observe a notable difference using the suggested parameters for our setting.
| **Optimizer** | **lr** | **eps** | **Test loss @15K** | **Test loss @30K** |
|:---:|:---:|:---:|:---:|:---:|
| Adam | 1e-3 | 1e-17 | 6.4120 | 6.2341 |
| Adam (Our settings) | 1e-4 | 1e-8 | 6.3102 | 6.2485 |
>**Performance Boost**
>I downloaded the code and ran it on a few benchmarks. I did not see a boost in modded-nanoGPT, which is a properly tuned baseline. I also did not see a boost vs Adam in some toy problems like xor
We would kindly ask the reviewer to elaborate on the details of their evaluation, as otherwise, we are unable to provide a proper response or explanation.
---
Rebuttal Comment 1.1:
Comment: Thank you for the experiments. I will certainly take them into consideration.
Here are the last two. Feel free to tune as much as you like.
Modded nanoGPT is the following benchmark. NanoGPT (124M) in 3 minutes. Can the authors run the 124M and the bigger benchmarks and report the results?
https://github.com/KellerJordan/modded-nanogpt
xor is the following benchmark. I tested the uploaded code, but I cannot seem to get Stacy to outperform Adam.
https://github.com/lixilinx/psgd_torch/blob/master/rnn_xor_problem_general_purpose_preconditioner.py
---
Reply to Comment 1.1.1:
Comment: The results of the 124M benchmark are as follows:
| **Optimizer** | **Val loss @0.2B tokens** | **Val loss @0.4B tokens** | **Val loss @0.6B tokens** | **Val loss @0.8B tokens** |
|:---:|:---:|:---:|:---:|:---:|
| AdamW | 4.715 | 4.055 | 3.853 | 3.765 |
| Stacey(p,p) | 4.157 | 3.887 | 3.762 | 3.688 |
We observe a notable improvement over AdamW, which is consistent with the LLM experiments in our paper. We set nearly all of the hyperparameters the same as listed in the paper for the LLM experiments with Stacey(p,p) (Table 7), except for $\alpha = 0.1$ and $\lambda = 0.001$.
We further wish to emphasize the overall contributions of our work, namely a primal-dual view of $\ell_p$ steepest descent that we justify both theoretically and empirically.
Having addressed these concerns and provided additional context for our contributions, we kindly ask the reviewer to reconsider their evaluation. | Summary: This paper introduces Stacey an optimisation algorithm targeted at training deep neural networks (DNNs). Stacey generalises SignSGD and conventional SGD, in a p-norm sense, where SGD uses the 2-norm to measure distance and SignSGD uses the inf-norm. On top of this Stacey include a acceleration scheme to aid the speed of convergence. The paper offers a theoretical result, specifically a convergence rate for an non-accelerated version of Stacey on smooth stochastic problems with bounded gradient and variance. Additionally there is an empirical evaluation of Stacey on standard DNN benchmarks against popular deep learning algorithms.
Claims And Evidence: The theoretical claims seem well supported.
The empirical claims are supported however I do have some doubts about the fairness of the empirical evaluation when comparing to other methods, however it is difficult to be totally objective here, given the natural differences between optimisers. Inevitably the wider community will need to judge how Stacey performs in practice compared to existing methods.
Methods And Evaluation Criteria: The benchmarks look appropriate, it would have been nice to see some smaller networks and more classical optimisation problems considered, given these don't take much compute.
Theoretical Claims: I did not thoroughly check the proofs due to time. The Theoretical Claims presented are not for Stacey but a far simpler non-accelerated algorithm.
Experimental Designs Or Analyses: The experimental design looks okay, though there are definitely some flaws here, see weakness section.
Supplementary Material: Yes experimental design section.
Relation To Broader Scientific Literature: The Relation To Broader Scientific Literature is well motivated.
Essential References Not Discussed: This recent paper is missing, and would be great to see included as a baseline, specially given its lower number of hyperparameters.
Defazio A, Yang X, Khaled A, Mishchenko K, Mehta H, Cutkosky A. The road less scheduled. Advances in Neural Information Processing Systems. 2024 Dec 16;37:9974-10007.
Other Strengths And Weaknesses: *Strengths*
1) The paper is well written.
2) The idea behind the paper seems neat and some related theoretical results are provided.
3) The benchmarks considered look appropriate, of course it would be nice to see more, including some more classical non-deep learning optimisation problems.
4) This seems a promising direction for further research to build on top of.
*Weaknesses*
1) The empirical experimental section has some flaws:
i) Some recent baselines are missing from the experimental section, specifically the one introduced last year in "The Road Less Scheduled"
ii) The amount of hyperparameters tuned for Stacey seems to far exceed the other methods, making the comparison hard to judge.
iii) It is not clear how robust Stacey is to its hyperparameters, nor how much hyperparameter tuning is required to get good results.
iv) There is lack of error bars or mention of variation between runs
v) Smaller scale classical optimisation problems are missing
vi) For the ImageNet results It is not clear why the results are presented at epoch 60 rather than the typical epoch 90 given at least some of the experiment were run for 90 epochs, as report in the appendix
vii) Tables of some results seem to be missing final, such as PPL on transformer pretraining.
viii) The number of iterations shown vary between plots for no explained reason.
ix) Some of the results for Stacey(2,2) seem to be different between plots (figure 5&6) & (figure 3 vs 11&12)
x) The transformer pertaining experiments seem to be missing some important details, model architecture what is LLama-100?, why test ppl increases, unexplained differences in performance between plots see point ix.
xi) Missing results for Stochastic ℓp Descent.
2) The totality of the above critics makes me wonder how much the results are being presented in a way to make them seem best. I would suggest spending a little more time in the appendix making it clear why specific choices were made. Without the empirical results the paper doesn't offer enough of a contribution in my opinion so it is essential a reader is not wondering why some seemly odd choice have been made in the way the experiments have been conducted and presented. My score is assuming greater clarity is given on the experiments in the final version of the paper.
3) The theoretical results are not presented for Stacey but a far simpler non-accelerated algorithm.
Other Comments Or Suggestions: It would be great to detail the grids searched over in terms of hyperparameters, not just the final values.
Some idea of the robustness of stacey to its hyperparameters would really help sell its practicality.
Please explain why the number of iteration at which results (both tables and plots) are shown seem to vary so much.
Questions For Authors: 1) Stacey has *a lot* of hyperparameters, many more than typically tuned for SGD and Adam, do you think your comparison is fair given this fact? Did you run a comparison where the same number of limited hyperparameters (say 1 or 2 only) are adjusted for all algorithms and the rest are left at their default values? Much of Adam (&AdamW) success is due to their robustness to it's hyperparamters, algorithms that need extensive hyperparameter tuning are unlikely to be used in practice. The experiments present in the paper do not make it clear to me how useful Stacey is as a practical algorithm.
2) The p norm used in Stacey is a hyperparameter, do you think it would be possible to adept Stacey to automatically work out the best setting of "p" for a given problem during the optimisation process? This would would help reduce the amount of hyperparamters required.
3) Further to the above, I understand the p norm used to measure distance in Stacey is fixed for all parameters, do you think it would be possible to extend stacey so it is adaptive adjusting the p-norm used, say per layer?
4) For some tasks Stacey(p,2) does better and some Stacey(p,p) does better what do you think might be causing this discrepancy?
5) Do you think Stacey with acceleration enjoys any theoretically properties? Did you make any progress to this end?
6) Is Stacey(p,p) equivalent to Stacey(p,2) and Stacey(2,p), If p = 2. If so, why do they seem to behave differently in your experiments?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful comments and suggestions, and we respond to their questions below.
> **Missing Reference**
Thanks for the suggestion. We will provide a citation and include it as a baseline in the updated manuscript.
> **Hyperparameters**
Though we may tune $\tau$ and $\alpha$, we found that, similar to SGD and Adam, the best choice comes from a small set, i.e., $\tau \in [0.001]$ and $\alpha \in [0.1, 0.01, 0.001]$, and so we believe this provides a fair comparison with other methods. We did run comparisons where a limited number of hyperparameters were tuned, while the rest were left at default values, as such defaults let us reduce the scope of the search.
> **Questions and Comments on Experiments**
> 1. Lack of error bars/variation
For space reasons, we kindly point the reviewer to our rebuttal for Reviewer ddGc for the tables of results with error bars.
> 2. Smaller scale classical optimisation problems are missing
While our method was designed with large-scale models in mind, we will include smaller scale experiments, and we would kindly ask the reviewer for suggested problems.
> 3. ImageNet result epochs
Thanks for catching this. This is a typo from an outdated table in the appendix, which we will update accordingly.
> 4. Tables of some results seem to be missing final
If we understand correctly, we will include tables of the PPL/transformer pretraining results, with error bars/variance included (as in the tables provided in the rebuttal).
> 5. The number of iterations shown vary
The iteration counts in Figures 2 and 4 differ because they represent two distinct experimental setups: one for ImageNet classification, the other for LLM pretraining, each with its own training configuration and iteration schedule.
> 6. x) The transformer pertaining experiments details
LLama-100 is adopted from the github repo of "GaLore: Memory-Efficient LLM Training by Gradient Low-Rank Projection" [Zhao et al. 2024]. The $p=3.3$ line's ppl increases because it is within a range that our algorithm cannot converge.
> 7. xi) Missing results for Stochastic ℓp Descent.
Stochastic lp descent is a special case of our algorithm; thus we have presented the better empirical versions of our algorithm (with acceleration), though we will include ablation studies in the updated manuscript.
> 8. (Q4) Stacey(p,2) vs. Stacey(p,p)?
Basing our intuition on the theory for the convex case, coupling a non-Eulidean primal with a Euclidean dual update (Theorem 1 in [Bai & Bullins 2024]), vs. non-Euclidean primal and dual updates (e.g. Theorem 2 in [Diakonikolas & Guzmán 2024]), leads to different trade offs between the problem geometry, initial iterate, and acceleration exponent, such that neither is uniformly better than the other.
> 9. (Q6) Stacey for p=2?
This occurs due to numerical differences from handling general $p$. However, we acknowledge this could cause confusion, so we will provide the algorithm for the simplified case of Stacey(2,2), along with a discussion of this distinction.
> **Choice of $p$**
> (Q2) automatically work out "p"?
One idea would be to use occasional Hessian information to adjust $p$ over time, based on the spectrum density [Ghorbani et al. 2019]. There has also been much work on developing automated means of hyperparameter tuning, including e.g. parameter-free methods [Jacobson & Cutkosky 2022], from which we hope to draw inspiration.
> (Q3) adjusting Stacey p choice per layer?
This is a wonderful suggestion. We may even benefit from a per-layer basis if we wished to leverage layer-wise Hessian information as a diagnostic tool (being far more compute-friendly).
> **Theoretical Properties of Stacey**
The acceleration framework of Stacey builds on linear coupling [Allen-Zhu & Orecchia, 2017], which is optimal in the first-order smooth and convex setting, and HASD [Bai & Bullins, 2024], which achieves faster convergence in the $\ell_p$ smooth non-Euclidean setting. Beyond the deterministic and convex regime, the core foundation of Stacey ---- non-convex stochastic $\ell_p$ steepest descent ---- achieves a first-order oracle complexity of $\mathcal{O}(\epsilon^{-4})$, which we discuss as tight in Section 4.1 and 4.2.
Providing a further theoretical characterization of Stacey’s acceleration remains challenging. Notably, even for widely used algorithms like Adam, existing theory typically shows only convergence or recovers first-order optimal regret, with limited formal evidence of superiority over other accelerated first-order methods. We suspect capturing the acceleration of Stacey in theory would require more refined and tailored assumptions. While we leave this as an open direction for future work, we highlight that Stacey generalizes both SignSGD and Lion ---- as discussed in the third paragraph of Section 4.2 ---- which suggests it offers greater flexibility and is more likely to admit improved theoretical properties. | Summary: This paper introduces **STACEY**, a novel optimization algorithm designed to accelerate stochastic steepest descent via ℓp-smooth nonconvex optimization. The key contributions of this work include:
- The development of **STACEY**, which incorporates primal-dual iterate interpolation to improve convergence rates for non-Euclidean smooth optimization problems.
- A theoretical framework that generalizes both SGD (when \( p = 2 \)) and signSGD (when \( p = \infty \)), with a **convergence guarantee of \( O(\epsilon^{-4}) \)** under standard assumptions.
- Empirical results demonstrating **superior convergence speed and final accuracy** compared to existing optimization methods, including SGD, Adam, AdamW, and Lion, on large-scale deep learning tasks such as image classification (CIFAR, ImageNet) and large language model (LLM) pretraining.
- A study on how different values of \( p \) affect performance, showing that non-Euclidean norms can be more effective in certain settings than traditional ℓ2-based methods.
The paper is **well-written, well-structured, and presents both strong theoretical contributions and compelling empirical results**.
Claims And Evidence: The paper makes several claims, all of which are generally well-supported:
- **Claim:** STACEY improves convergence rates over traditional SGD and adaptive optimizers.
**Evidence:** Empirical evaluations on CIFAR, ImageNet, and LLM pretraining demonstrate improved speed and final accuracy.
- **Claim:** The proposed method generalizes previous optimization approaches by considering a broader class of ℓp-norms.
**Evidence:** Theoretical analysis rigorously proves this generalization.
- **Claim:** STACEY benefits from the flexibility of choosing different \( p \) values.
**Evidence:** Experiments with different values of \( p \) show that problem-specific norm choices can yield better performance.
One area where **the claims could be strengthened** is in providing a more detailed computational complexity comparison to confirm the practical efficiency of STACEY in large-scale settings.
---
Methods And Evaluation Criteria: The methods and evaluation criteria are **appropriate and well-justified**:
- **Optimization Benchmarks:** The paper evaluates STACEY on well-established benchmarks, including CIFAR-10, ImageNet, and LLM pretraining tasks.
- **Comparisons:** The algorithm is compared against widely used optimizers (SGD, Adam, AdamW, Lion), which are the **correct baselines** for this type of work.
- **Evaluation Metrics:** The paper reports **training loss, test accuracy, and convergence speed**, which are standard and relevant evaluation criteria for optimization algorithms in deep learning.
However, **an additional runtime or computational cost comparison** would be useful to fully assess the trade-offs of using STACEY in practice.
---
Theoretical Claims: I reviewed the theoretical claims and found them **mostly sound**:
- The **convergence proof for stochastic ℓp steepest descent** follows standard assumptions and **logically extends previous results**.
- The **use of primal-dual interpolation** is well-motivated, and the acceleration rate follows existing literature on non-Euclidean acceleration.
- The **generalization to different ℓp norms** appears correct and aligns with prior research on optimization under non-Euclidean norms.
One possible **area for clarification** is the effect of different values of \( p \) on the acceleration exponent. **An intuitive explanation of how acceleration scales with \( p \) would improve clarity.**
---
Experimental Designs Or Analyses: The **experimental design is well-structured**, with meaningful comparisons. I verified the validity of:
- **Image classification experiments** on CIFAR and ImageNet.
- **LLM pretraining experiments** on the C4 dataset.
- **Ablation studies** exploring the role of \( p \).
Potential improvement:
- A **detailed analysis of computational efficiency (runtime per iteration, memory overhead, etc.)** would make the comparisons more complete.
- It would be useful to explore **STACEY’s performance in additional non-Euclidean problems**, such as adversarial training or reinforcement learning.
---
Supplementary Material: The supplementary material includes **code, additional proofs, and extra experimental results**. I reviewed:
- **Appendix A:** Detailed proofs of convergence rates.
- **Appendix D:** Hyperparameter tuning strategies.
These sections **add depth to the paper** and support the claims made in the main text.
---
Relation To Broader Scientific Literature: This paper is **well-grounded in prior research** on stochastic optimization and non-Euclidean geometry in machine learning:
- It builds upon **SGD (Robbins & Monro, 1951), signSGD (Bernstein et al., 2018), and AdamW (Loshchilov & Hutter, 2019)**.
- It connects with recent studies on **non-Euclidean optimization (Diakonikolas & Guzmán, 2024)** and **adaptive gradient methods**.
- The idea of **primal-dual interpolation** is influenced by **work on non-Euclidean acceleration (Allen-Zhu & Orecchia, 2017; Nemirovskii & Nesterov, 1985)**.
This paper **extends these ideas in a meaningful way**, demonstrating both theoretical and empirical improvements.
---
Essential References Not Discussed: The paper **covers most essential references**, but **a comparison with curvature-aware optimizers (e.g., Shampoo, K-FAC)** would be useful. These methods also attempt to handle **non-Euclidean optimization challenges**, making them relevant to the discussion.
I recommend citing **Gupta et al. (2018) on Shampoo** and **Martens & Grosse (2015) on K-FAC** to highlight how STACEY differs from these approaches.
---
Other Strengths And Weaknesses: ### **Strengths**
- **Strong theoretical foundation** with **generalized convergence guarantees**.
- **Comprehensive empirical validation** showing consistent improvements over baselines.
- **Clear writing and structured explanations**.
### **Weaknesses**
- **No computational cost analysis** (memory and runtime comparisons are missing).
- **Hyperparameter selection for \( p \) is unclear** (no systematic guidance provided).
- **Missing comparisons with curvature-aware optimizers** (e.g., Shampoo, K-FAC).
---
Other Comments Or Suggestions: - **Clarify the intuition behind acceleration for different values of \( p \)**.
- **Include an ablation study on the effect of different values of \( p \) on generalization performance**.
- **Discuss whether STACEY could be extended to second-order methods or mixed-order approaches**.
---
Questions For Authors: 1. **How does the per-iteration computational cost of STACEY compare to SGD, Adam, and Lion in terms of runtime and memory consumption?**
2. **Could you provide a practical heuristic or automated procedure for selecting \( p \) in different tasks?**
3. **How does STACEY perform when compared to second-order methods like Shampoo or K-FAC? Would these methods benefit from a similar ℓp-based approach?**
---
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their thoughtful comments and suggestions, and we respond to their questions below.
> Detailed **computational complexity in terms of runtime and memory consumption** compared to SGD, Adam, and Lion
**Runtime**
Let $d$ be the number of parameters, and let each “basic operation” refer to simple scalar arithmetic (e.g., an addition, multiplication, or sign). We will ignore lower-level details (e.g., hardware vectorization) and focus on how many scalar operations are performed per parameter per iteration.
**SGD**
Key steps:
1) $m_i \leftarrow \beta m_i + (1-\beta)\nabla_i \quad (\text{2 multiplications, 1 addition})$.
2) $x_i \leftarrow x_i - \alpha m_i \quad (\text{1 multiplication, 1 addition})$.
Approximate ops per parameter: ~5–6 scalar ops (fewer if no momentum is used).
**Adam**
Key steps:
1) $m_i \leftarrow \beta_1 m_i + (1-\beta_1)\nabla_i
\quad (\text{2 multiplications, 1 addition})$.
2) $v_i \leftarrow \beta_2 v_i + (1-\beta_2)\nabla_i^2
\quad (\text{3 multiplications, 1 addition})$.
3) $x_i \leftarrow x_i - \alpha\frac{m_i}{\sqrt{v_i} + \epsilon}
\quad (\text{1 square root, 1 division 1 multiplication, 1 addition})$.
Approximate operations per parameter: ~9–12 scalar ops (slightly more if you count the bias-correction steps separately).
**Lion**
Key steps:
1) $m_i \leftarrow \beta m_i + (1-\beta)\mathrm{sign}(\nabla_i)
\quad (\text{2 multiplications, 1 addition, 1 sign operation})$.
2) $x_i \leftarrow x_i - \alpha\,\mathrm{sign}(m_i) \quad (\text{1 sign, 1 multiplication, 1 addition})$.
Approximate operations per parameter: ~6–7 scalar ops (including sign as an operation).
**Stacey**
Key steps:
1) Update the “momentum-like” buffer $m_i$ (coordinate-wise re-scaling).
2) Update the dual vector $z_i$ (coordinate-wise multiplications/additions).
3) Combine $m_i$ and $z_i$ to get the final parameter update.
Representative breakdown:
1) Update $m_i$: ~3–5 ops.
2) Update $z_i$: ~3–4 ops (coordinate-wise re-scaling plus addition).
3) Final parameter update: ~2–3 ops (linear combination and one addition/subtraction).
Approximate operations per parameter: ~9–12 scalar ops.
**Memory Footprint**
**SGD**:Momentum buffer (if used). Total auxiliary overhead: $d$
**Adam**: First moment and second moment. Total auxiliary overhead: $2d$
**Lion**: Momentum-like buffer. Total auxiliary overhead: $d$
**Stacey**: Momentum-like buffer and dual vector. Total auxiliary overhead: $2d$
Thus, Stacey’s memory requirement is similar to Adam, and slightly more than other single-pass gradient methods (though we note that its overhead compared to e.g. SGD, Lion comes precisely from the additional dual vector).
> **Choice of $p$: intuition, ablation, practical heuristics**
Although it can be challenging to provide intuition for acceleration (even in the convex $p=2$, i.e. Nesterov's, case), at a high level the analysis carefully balances the primal and dual updates, leveraging the uniform convexity of $\|\cdot\|_p^p$ and an alternative smoothness-derived upper bound, as in Definition 2 and Lemma 1 in [Diakonikolas & Guzmán 2024]. We will include an ablation study of the influence of $p$ on the acceleration rate in the updated manuscript, to help provide additional insight for these theoretical results.
Regarding heuristics for choosing $p$, one idea would be to use occasional Hessian information to determine how to adjust $p$ over time, based on the spectrum density [Ghorbani et al. 2019]. Additionally, there has been much work on developing automated means of hyperparameter tuning, including e.g. parameter-free methods [Jacobson & Cutkosky 2022], from which we may hope to draw inspiration.
> **Second-order curvature-aware optimizers: citations and discussion**
We thank the reviewer for pointing out these helpful references. We will cite them and incorporate the following discussion in the revised version. Shampoo [Gupta et. al., 2018], K-FAC [Martens & Grosse, 2015] and their follow-ups are indeed representative works of curvature-aware optimization methods. One notable difference is that these works are second-order methods that exploit the structure of the Hessian or Fisher information and focus on techniques for their efficient approximation, whereas our method, Stacey, is a first-order approach that explores non-Euclidean geometry though a differing $\ell_p$ norm. We will include comparisons with these curvature-aware optimizers in the updated version of our manuscript.
Extending Stacey to second-order methods is, in our view, a promising direction that aligns with our own considerations for future research as well. It is natural to investigate the non-Euclidean counterpart of a preconditioned gradient step, just as we have done in the first-order setting. Such a method holds the potential to benefit from both the curvature awareness provided by the Hessian information and the geometric advantages of operating under a differing $\ell_p$ norm. | null | null | null | null | null | null | null | null |
A Physics-Augmented Deep Learning Framework for Classifying Single Molecule Force Spectroscopy Data | Accept (poster) | Summary: This paper presents a machine learning-based approach for classifying single-molecule force spectroscopy (SMFS) data from protein unfolding experiments. Specifically, the model distinguishes force measurements originating from valid single-molecule unfolding events versus artifacts. While ML-based classification of SMFS data has been explored in prior work, the novelty of this paper lies in leveraging a synthetic dataset of simulated force curves to train the classifier. The study evaluates the model’s performance on three different proteins: Titin, utrophin, and dystrophin.
Claims And Evidence: - The paper introduces an important and impactful task to the ML research community, particularly in the domain of SMFS data analysis.
- The study is well-motivated, providing a clear explanation of how classifying force curves can help automate data filtering in protein unfolding experiments.
- The experimental design is rigorous, incorporating statistical significance assessments to support conclusions.
- The paper provides evidence that classifiers trained on synthetic data generalize well to experimental force curves, reducing the need for large labeled experimental datasets.
Methods And Evaluation Criteria: - **Novelty in Methodology:** While the application of ML to SMFS data is valuable, the ML techniques employed are relatively standard, with no major methodological innovations beyond dataset generation. The primary novelty lies in the application to non-specific pulling data rather than the model design itself.
- **Evaluation Scope:** The reviewer initially raised concerns about whether the task is inherently simplified due to the presence of repeated structures in proteins. The authors clarified that only one of the three proteins (Titin) exhibits this characteristic, while dystrophin and utrophin contain heterogeneous domains. This addresses part of the concern, though further discussion on how different domain structures affect classification performance would strengthen the contribution.
- **Potential Limitations in Practical Use:** While the authors argue that non-specific pulling is more prevalent and accessible, additional discussion on potential trade-offs compared to specific pulling methods would be valuable. For instance, how does classification accuracy compare between non-specific and specific pulling data, and could certain experimental conditions confound classification?
Theoretical Claims: N/A
Experimental Designs Or Analyses: The paper presents a well-structured experimental design, particularly in training the classifier using a Monte Carlo simulation engine to generate synthetic SMFS datasets. The approach ensures that both single-molecule and multi-molecule scenarios are included in the training data, making the classifier robust to experimental conditions. However, additional analysis on how well the synthetic data mimics real-world experimental variations (e.g., environmental noise, instrument precision) would be beneficial. The experimental validation, achieving 79.6% accuracy on real data, suggests the method is effective, but further discussion on the biological implications of misclassified events would strengthen the paper.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper contributes to the ongoing efforts in automating protein folding and unfolding analysis using machine learning. Prior work has applied ML models to classify SMFS data, but this study is distinctive in its use of a dual-branch fusion model incorporating physical constraints. The approach aligns with the broader trend of integrating domain knowledge into deep learning models, a strategy seen in fields such as structural biology and molecular modeling. Additionally, the use of synthetic data for training is increasingly common in other biological data processing tasks, such as cryo-EM image classification and protein structure prediction.
Essential References Not Discussed: The paper should consider citing prior works on ML-based classification of SMFS data, particularly those that use conventional feature engineering or statistical methods to distinguish single-molecule events. Additionally, recent advances in physics-informed deep learning models could be relevant, as they demonstrate similar techniques of integrating domain-specific constraints into deep networks.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: - The classification task may be relatively simple if the primary distinguishing feature is the presence of repeated patterns in force curves. The authors partially address this by noting that real-world noise, heterogeneity in protein structure, and environmental factors make classification challenging. Additional ablation studies isolating these factors would provide deeper insights.
- Some figures and explanations could be clearer, particularly in illustrating how synthetic data is generated and validated against real experimental data.
Questions For Authors: - Can the classifier generalize to other proteins beyond the three tested? If so, what are the expected limitations?
- What are the dominant features learned by the classifier? Are they interpretable in a biophysical sense?
- Does the medium in which force measurements are taken (e.g., buffer conditions) influence classification accuracy? If so, how does the model handle such variations?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. We address your concerns below and welcome further discussion. If there are no additional issues, we would appreciate your consideration in raising our score.
**A Challenging Problem:** Our lab studies novel molecules like dystrophin and utrophin to understand their mechanical properties. Initially, isolating single-molecule pulling trials was a manual, time-intensive process, requiring a full day per experimental iteration of a specific molecule. Multiple iterations are the norm in this area. Moreover, no repeated pattern is known or present to isolate data resulting from single molecule. Challenges include heterogeneity of domains, low signal to noise ratios, instrument and thermal noise, unfolding domain uncertainty, and stochastic unfolding forces. These complexities make automated classification both difficult and essential.
**Novelty:** We gently but firmly disagree with the reviewer on the novelty. First, our domain expertise in SMFS was crucial in identifying the right problem for an impactful ML application. Second, while standard ML methods perform well on large datasets, SMFS has limited training data. To address this, we introduced a novel dual-branch ML architecture incorporating protein unfolding physics, a unique approach enabled by SMFS expertise.
**Practical Use and Generalization:** Specific pulling requires functionalized cantilevers and tailored molecular fingerprints, making it a time-consuming, protein-specific process. While these fingerprints help classification, they introduce artifacts, as these domains do not exist in native proteins. In contrast, non-specific pulling avoids these modifications, making it more accessible but harder to classify. Our ML based approach overcomes these challenges while preserving the advantages of non-specific pulling.
Even without ML, comparing specific and non-specific pulling data is complex, requiring tailored fingerprints and biochemical adjustments for each protein—a challenge beyond this article’s scope. Our lab is among the few capable of purifying dystrophin and utrophin, yet no specific pulling data currently exists for these proteins due to experimental complexity (design and execution of experiments for specific pulling need to be done separately for each protein and are quite involved). We are actively working to collect this data and plan to apply our methods upon availability.
PemNN outperforms baselines by 11.4% with only ~30 experimental training samples. Even without experimental training data, it achieves average accuracies of 72.0% $\pm$ 5.9% through pre-training simulated datasets. To test generalizability, we applied our method to two newly investigated proteins (full-length utrophin and dystrophin) using transfer learning with only ~30 experimental samples, achieving 79.4% $\pm$ 4.8% accuracy over five runs. Our approach has streamlined analysis and reduced processing time to under an hour, significantly improving efficiency over traditional methods. Our method focuses on isolating trials from single molecule, which comes into play after the biochemistry (buffer conditions) is already decided. Thus, these factors will have minimal impact on our classification accuracy.
**Comparison to non-ML methods:** Please refer to Reviewer 7QeU item 5.
**Experimental vs. simulated data:** We compared unfolding forces from experimental and simulated data based on their most probable values and interquartile ranges (IQR) (see Table). Most probable values closely match, with differences from 2 pN (Titin I27O) to ~10 pN (10%) (Bact UtrN-R3, Insect UtrN-R3, DysN-R3), indicating reasonable simulation accuracy. The IQR discrepancy likely arises from using a single double-well potential for domains in simulations. Notably, models pre-trained on homogeneous simulated data effectively classify experimental data with heterogeneous domains. We will incorporate this discussion in our revised paper.
| | Titin I27O | Bact UtrN-R3 | Insect UtrN-R3 | DysN-R3 |
|:----------:|:--------------------:|:-------------------:|:---------------------:|:-------------------:|
| Exp | 216(50) | 82(64) | 89(71) | 91(66) |
| Sim | 218(36) | 85(22) | 97(40) | 80(25) |
Our classification method is not error-free, so in practice, we manually inspect filtered datasets using domain expertise. However, our approach reduces dataset size to 5–10% of the original, making manual review far more efficient.
**Reference:** Due to space constraints, we highlight the most relevant study. [1] applied ML to SMFS specific pulling data to identify single molecule data; specific pulling results remain relevant and limited to the protein being investigated and do not generalize to other proteins. Our emphasis is non-specific pulling, which is more generalizable across proteins.
[1] Waite et al., Patterns 4.1 (2023). | Summary: The authors propose a physics-inspired architecture to classify single molecule events from force spectroscopy data. They provide datasets, including simulations, to evaluate their method compared to previous baselines showing improved performance.
Claims And Evidence: - The proposed model outperforms baselines: this claim seems to be adequately confirmed by the experimental evaluations
- The physics-informed module improves performance: this seems to be supported by ablations in Fig. 5 / comparisons to baselines
Methods And Evaluation Criteria: The authors create a simulated dataset that seems relevant for evaluating the models. I am not familiar enough with this field to comment on whether the experimental datasets considered make sense for the problem set up, but they seem reasonable.
Theoretical Claims: n/a
Experimental Designs Or Analyses: The main concern I have with the experimental design is the train/test split of 20/80. While I understand that in practice there may be very limited training data for the application area, it could still be interesting to evaluate the models with the larger amounts of training data available. For instance, I would be curious to see what Fig. 6 looks like if it is extended up to 80% of the training data.
Supplementary Material: I looked at the supplemental code.
Relation To Broader Scientific Literature: This paper seems relevant to the SMFS community to decrease the amount of manual labor needed to classify force curves.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: The paper is in general well written. The paper could benefit from slightly more detailed justification of the model architecture in the main text. Although I know that many of these points are addressed in the appendix, at least mentioning them in the main text could be useful for the reader (i.e. choice of 3 classification targets instead of 2, choice of PEM model, etc).
Other Comments Or Suggestions: n/a
Questions For Authors: - Why are other more modern sequence modeling architectures used (i.e. Transformer) instead of an LSTM?
- Could more detail be provided on the polymer elastic model branch? Are the predicted contour lengths simply passed in to the fusion block as a physics-augmented feature?
- Are there standard non-ml baselines that are relevant to include for this field?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. We have addressed your questions and concerns below. If there are any remaining issues, we would be happy to discuss them further. If there are no additional concerns, we would appreciate your consideration in raising our score.
1. *The main concern I have with the experimental design is the train/test split of 20/80.*
**Author response**:
As suggested by you we have tested our model and baseline methods using different train/test splits on experimental datasets. The table below presents the mean accuracy (with standard deviations in parentheses) across all experimental datasets over five runs.
| Train/Test Ratio | 5/80 | 40/60 | 60/40 | 80/20 |
|:--------------------:|:-------------------:|:-------------------:|:-------------------:|:-------------------:|
| PemNN | 79.61(5.24) | 86.82(4.86) | 88.50(5.09) | 88.54(5.68) |
| LSTMFCN | 68.26(12.12) | 85.12(7.49) | 85.51(6.87) | 87.66(7.66) |
| ResNet | 37.47(6.33) | 81.01(9.13) | 84.62(7.13) | 84.47(9.26) |
| FCN | 35.88(7.37) | 75.50(8.92) | 75.48(13.15) | 79.43(10.18) |
| Triplet | 55.58(10.17) | 66.78(12.06) | 69.15(12.26) | 66.92(11.45) |
| InceptionTime | 35.32(3.97) | 80.78(12.78) | 81.35(9.07) | 84.76(11.58) |
Our method shows particular advantage when the training data is limited, achieving at least 11.4% higher average accuracy compared to baseline methods. Even with increased training data, our approach maintains superior accuracy while exhibiting smaller standard deviations. We appreciate your suggestion and will incorporate this discussion into the revised manuscript.
2. *The paper could benefit from slightly more detailed justification of the model architecture in the main text.*
**Author response**:
Thank you for your suggestion. We will incorporate relevant details from appendix including your suggestions into the main text of the revised manuscript.
3. *Why are other more modern sequence modeling architectures used (i.e. Transformer) instead of an LSTM?*
**Author response**:
Thank you for your question! We chose to use an LSTM because it is well-suited for sequential data where temporal dependencies need to be captured. Furthermore, earlier studies have shown that augmenting convolutional layers with LSTM significantly improves performance in time series classification with only a modest increase in the number of parameters [1,2,3]. However, we will be exploring more modern sequence modeling architectures in future work to assess potential performance improvements.
4. *Could more detail be provided on the polymer elastic model branch?*
**Author response**:
We provide a detailed description of the polymer elastic model branch here. Given i-th force curve of length $T^{(i)}$, consisting of force data $\mathcal F^{(i)}=[F_1^{(i)},F_2^{(i)},…,F_{T^{(i)}}^{(i)}]$ and extension data $\mathcal X^{(i)}=[X_1^{(i)},X_2^{(i)},…,X_{T^{(i)}}^{(i)}]$, the corresponding contour length ${L_c}_p^{(i)}$, for $p=1,2,…,T^{(i)}$, is computed using polymer elastic models. A subsequent filtering step selects P samples with ${L_c}_p^{(i)}\in [0,M]$, where M is the filter threshold. If the number of qualified data points is less than P, sampling is performed with replacement. The filtered data, $[F_1^{(i)},F_2^{(i)},…,F_P^{(i)}; {L_c}_1^{(i)},{L_c}_2^{(i)},…,{L_c}_P^{(i)}]$, is processed through convolutional blocks and the LSTM layer in the physics-based branch.
5. *Are there standard non-ml baselines that are relevant to include for this field?*
**Author response**:
Currently, manual visual inspection remains the primary method for classifying force curves resulting from single proteins [4,5]. Different labs often develop their own heuristic methods to analyze single molecule data, as illustrated in [6,7]. Even though such heuristic methods can analyze data, they are approximate and require an expert to manually adjust the parameters. We provided a comparison to these non-machine learning methods on our four protein molecules (supplementary material in Section 6.5 on Page 8 and Appendix D.4 on Page 20), we showed that our model can effectively analyze AFM data by accurately capturing key statistical features while effectively filtering out confounding factors from multiple molecules.
[1] Karim et al., Neural Networks 116 (2019)
[2] Zhang et al., AAAI 34(04) (2020)
[3] Hewamalage et al., Int. J. Forecast. 37(1) (2021)
[4] Bornschlögl & Rief, Single Molecule Analysis (2011)
[5] Ares et al., Nanoscale Imaging (2018)
[6] Ramirez et al., J. Biol. Chem. 299(2) (2023)
[7] Rajaganapathy et al., Sci. Rep. 9(1) (2019)
---
Rebuttal Comment 1.1:
Comment: I appreciate the response from the authors. The fact that the difference in performance disappears with more training data slightly worries me. At a minimum, this analysis should be included in the main text. This might also indicate that the evaluation setup might need to be reconsidered. Importantly, non-deep learning-based ML baselines might perform quite well with such limited data (30 to 120 samples). I also do not have the domain expertise to comment on whether the difference between the heuristic approach and the proposed method presented in Fig. 7 is meaningful. In general, I think the paper is well-written, but I agree with Reviewer V7uf that (1) none of the reviewers seem to have the domain expertise to properly evaluate the whole paper and (2) the ML innovation is limited. A different audience might be able to better review and appreciate the results and work from the authors.
---
Reply to Comment 1.1.1:
Comment: Proteins exhibit significant diversity in their structure and mechanical properties. As presented earlier, there is a need to classify if the protein trial results from a single molecule or not. To develop such an automation tool, we distilled the biological relevant questions to be posed in a machine learning framework and applied state-of-the-art machine learning models (such as ResNet, FCN, InceptionTime, and LSTMFCN) to SMFS data, marking the first known application of these deep learning methods in this domain; application of these ML methods is also a contribution of this article.
While it is possible to build a highly generalizable model that can handle a wide variety of proteins, doing so would require computational resources comparable to those used by models like AlphaFold, which is beyond the scope of our study. Instead, given a day of SMFS experimental data on newly studied protein, our goal is to develop an automation tool that can efficiently classify the experimental data while requiring fewer than 50 labeled training samples. Motivated by the limited availability of labeled training data, we innovated a dual branch machine learning architecture with the incorporation of physics of protein molecules unfolding. While some state-of-the-art non-deep learning approaches may outperform deep learning models in certain scenarios, they often come with prohibitively high computational complexity and training time requirements [1,2,3]; this is also our experience in our own research. Taking these factors into account, we provide a practical, efficient, and high-performing approach tailored specifically to SMFS data. The machine learning automation has become a part of our workflow in investigating utrophin and dystrophin and in the general study of muscular dystrophin. We therefore are confident that these techniques will be useful to other SMFS areas as well.
We applied our method, along with non-machine learning approaches, to analyze data from Titin I27O, a well-calibrated protein molecule with a most probable unfolding force of 204±26 pN. Our method achieved a most probable unfolding force of 206.68 pN (Figure 7), closely aligning with the expected value. In contrast, the non-machine learning methods (RawData and Heuristic) exhibited greater deviations from 204 pN. Furthermore, the inclusion of data not originating from single-molecule events resulted in broader force distributions. We quantified the sharpness of these distributions using the interquartile range (IQR), as listed in Table 4 (Page 22). Our method achieved an IQR of 52.63, which is only a quarter of the IQR observed in non-machine learning methods, effectively filtering out confounding factors.
Below is a description of the overall contribution of this article which we provided to the ACs in the original submission.
*Traditionally, isolating single-molecule pulling trials was a manual, time-intensive process, requiring a full day per experimental iteration of a specific molecule. Typically, multiple iterations are the norm in this area. Challenges such as domain heterogeneity, low signal-to-noise ratios, instrument and thermal noise, and stochastic unfolding forces make automation both difficult and essential.*
*Our work is the first to apply state-of-the-art machine learning models (such as ResNet, FCN, InceptionTime, and LSTMFCN) to SMFS data. Additionally, we introduced a novel dual-branch ML architecture incorporating protein unfolding physics, a unique approach enabled by SMFS expertise that outperforms baseline models. Furthermore, we provide a Monte Carlo simulation engine to generate force spectroscopy datasets alongside extensive experimental data from atomic force microscopy on a variety of proteins. We believe our work further opens up a new area for ML researchers with new datasets, simulation engines, and ML algorithms toward the important area of single molecule research and in particular single molecule force spectroscopy research.*
[1] Ismail Fawaz, Hassan, et al. "Deep learning for time series classification: a review." Data mining and knowledge discovery 33.4 (2019): 917-963.
[2] Middlehurst, Matthew, et al. "HIVE-COTE 2.0: a new meta ensemble for time series classification." Machine Learning 110.11 (2021): 3211-3243.
[3] Ismail Fawaz, Hassan, et al. "Inceptiontime: Finding alexnet for time series classification." Data Mining and Knowledge Discovery 34.6 (2020): 1936-1962. | Summary: The paper introduces Polymer Elastic Models Neural Networks (PemNN), a deep learning model designed to classify molecular force curves as originating from no molecule, single molecule or multiple molecules.
Claims And Evidence: Yes, the claims are supported by clear evidence.
Methods And Evaluation Criteria: Yes, the evaluation methods make sense for supporting the claims.
Theoretical Claims: The paper introduces no theoretical claims.
Experimental Designs Or Analyses: Yes, I checked the soundness of the experimental setup.
Supplementary Material: I have not reviewed the supplementary material
Relation To Broader Scientific Literature: I am only familiar with the literature in the field of machine learning. The method uses existing building blocks to create an globally novel architecture.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
* The descriptions of the experimental setup and of the methods are particularly clear.
* The statistical significance of the results is always shown clearly.
Other Comments Or Suggestions: * Figure 4: what do the numbers represent?
* Figure 5: Different method are hard to distinguish in the radar plot. Could the authors use a bar plot or a line plot instead?
Questions For Authors: No additional questions
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. We have addressed your questions and concerns below. If there are any remaining issues, we would be happy to discuss them further.
1. *Figure 4: what do the numbers represent?*
**Author response**:
We use classification accuracy as the metric to compare the performance of different models, including our model PemNN and five baseline models, across multiple datasets. Per each dataset, we evaluated all models on testing data and ranked them based on their mean classification accuracy over five runs, assigning a rank of 1 to the most accurate model and 6 to the least accurate. The average ranking is then computed across all datasets, including both simulated and experimental testing sets for all protein molecules. The average ranking for each model is presented in the critical difference diagram [1], as presented in Figure 4. PemNN achieves the lowest ranking of 1.4167, indicating that our model is more accurate than baseline models.
To assess statistical significance, we conducted the Wilcoxon signed-rank test with Holm correction as a post-hoc test following the Friedman test [1,2]. In Figure 4, thick horizontal lines represent groups of models that are not significantly different in terms of classification accuracy. From Figure 4, we conclude that PemNN is significantly more accurate than all baseline models. Among the baselines, LSTMFCN has the lowest rank, with its performance statistically similar to ResNet and FCN (as indicated by the thick horizontal line connecting these three models).
2. *Figure 5: Different methods are hard to distinguish in the radar plot. Could the authors use a bar plot or a line plot instead?*
**Author response**:
Thank you for your suggestion. We acknowledge that distinguishing between different methods may be challenging in the current format. To improve clarity, we will replace the radar plot with a bar plot or a line plot in our revised paper.
[1] Demšar, Janez. "Statistical comparisons of classifiers over multiple data sets." Journal of Machine learning research 7.Jan (2006): 1-30.
[2] Ismail Fawaz, Hassan, et al. "Deep learning for time series classification: a review." Data mining and knowledge discovery 33.4 (2019): 917-963. | Summary: this work proposes a deep learning model to classify SMFS curves.
the model consists of two branch, one is "based on physics" and another is called "force-trace", followed by fusion modules.
their experiments show improved accuracy.
Claims And Evidence: they claimed "superior performance compared to sota baseline methods"
the results illustrated in Fig 6 however seems to question statistical significance, as indicated by overlapping error bars.
Methods And Evaluation Criteria: the two-branch design seem to make sense to me, but it will be more convincing if the ablation study, e.g., one-branch vs two-branch, is presented.
Theoretical Claims: N/A
Experimental Designs Or Analyses: looks good to me
Supplementary Material: N/A
Relation To Broader Scientific Literature: wondering what the broader community can learn from this work.
I wish to see evidence that the architecture brings insights that can be applied not only on SMFS
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: see above (statistical significance, ablation study, broader impact)
Other Comments Or Suggestions: see above
Questions For Authors: see above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback. We have addressed your questions and concerns below. If there are any remaining issues, we would be happy to discuss them further. If there are no additional concerns, we would appreciate your consideration in raising our score.
We would like to emphasize that our article is the first to apply state-of-the-art machine learning models (ResNet, FCN, InceptionTime, and LSTMFCN) to Single Molecule Force Spectroscopy (SMFS) data. Additionally, we introduce PemNN, a novel model specifically designed for this domain, which outperforms baseline models. Furthermore, we provide a Monte-Carlo simulation engine and extensive datasets generated from atomic force microscopy experiments on a variety of proteins.
1. *they claimed "superior performance compared to sota baseline methods" the results illustrated in Fig 6 however seems to question statistical significance, as indicated by overlapping error bars.*
**Author response**:
Figure 6 reports mean accuracy and standard deviations across all experimental datasets, with each dataset evaluated over five runs. PemNN outperforms ResNet, FCN, Triplet, and InceptionTime without overlapping error bars. While some overlap exists with LSTMFCN at training sizes 0.1, 0.15, and 0.2, PemNN maintains higher mean accuracy. To further assess the statistical significance, we conducted the Wilcoxon signed-rank test with Holm correction as the post-hoc test following the Friedman test [1,2]. The results are visualized in the Critical Difference (CD) diagram [1] in Figure 4, where thick horizontal lines indicate groups of classifiers that are not significantly different in terms of accuracy. In this diagram, our method is ranked significantly higher than the baseline methods.
2. *the two-branch design seem to make sense to me, but it will be more convincing if the ablation study, e.g., one-branch vs two-branch, is presented.*
**Author response**:
Thanks for your comment. Indeed, we have evaluated the efficacy of two branches (force trace branch and physics-based branch) vs a single branch in Section 6.3 (Page 7) of our submitted paper. We showed that the physics-based branch enhances performance by incorporating polymer elastic models. Furthermore, the force trace branch enhances robustness against parameter errors. By combining the strengths of both branches, PemNN consistently outperformed baselines in SMFS classification tasks, demonstrating its effectiveness under various conditions.
3. *wondering what the broader community can learn from this work. I wish to see evidence that the architecture brings insights that can be applied not only on SMFS*
**Author response**:
SMFS is crucial in understanding protein folding and unfolding which is of vital importance for human biology and health; a cursory investigation on the internet can provide evidence of the journals and research in this area. Machine Learning has the potential to substantially revolutionize this area with public datasets and associated ML based methods, mirroring the impact that ML has already had across other scientific domains.
The many existing multivariate time-series classification models attempt to capture relationships across different input channels [3,4]. While biological data often exhibit an interdependency that can be modeled as nonlinear functions among multiple variables. Our method leverages the relationship between extension and force through the polymer elastic model in the physics-based branch. The exploration of cooperative features among biological data could extend beyond SMFS, offering a broader impact on multivariate time-series analysis in other biological domains; however, this is outside the scope of the present article.
As alluded to earlier, our work provides (1) a new ML model, PemNN (2) a Monte-Carlo based simulation engine (3) SMFS experimental datasets for a variety of proteins (4) application of prior state-of-the-art ML models to SMFS data. We hope that the reviewer finds the scope of work, its innovations, and the potential avenues it opens for future research, convincing.
[1] Demšar, Janez. "Statistical comparisons of classifiers over multiple data sets." Journal of Machine learning research 7.Jan (2006): 1-30.
[2] Ismail Fawaz, Hassan, et al. "Deep learning for time series classification: a review." Data mining and knowledge discovery 33.4 (2019): 917-963.
[3] Zheng, Yi, et al. "Exploiting multi-channels deep convolutional neural networks for multivariate time series classification." Frontiers of Computer Science 10 (2016): 96-112.
[4] Zhang, Xuchao, et al. "Tapnet: Multivariate time series classification with attentional prototypical network." Proceedings of the AAAI conference on artificial intelligence. Vol. 34. No. 04. 2020. | null | null | null | null | null | null |
RepoAudit: An Autonomous LLM-Agent for Repository-Level Code Auditing | Accept (poster) | Summary: This paper presents REPOAUDIT, a system for auditing source code using large language models to identify and report software bugs. The system is designed to detect common vulnerabilities such as null pointer dereferencing, memory leak, and use after free. It utilizes a combination of parsing libraries, large language models, and a multi-step exploration process to identify potential bugs within software repositories. The system was tested against several real-world projects and compared to existing auditing methods.
Claims And Evidence: The paper demonstrates an innovative approach by leveraging LLMs like Claude 3.5 Sonnet to perform data-flow analysis and control-flow validation, which significantly enhances bug detection. The system's ability to detect inter-procedural bugs is a notable strength, as demonstrated by the high number of true positive results, particularly for cross-function vulnerabilities.
Methods And Evaluation Criteria: The authors introduce two important validation mechanisms—alignment validation of data-flow facts and control flow, and feasibility validation of inter-procedural program paths. These mechanisms help ensure the accuracy of bug reports, reducing the likelihood of false positives and increasing the reliability of the tool.
While the paper focuses on three bug types (NPD, MLK, and UAF), it does not address how REPOAUDIT can handle a broader range of vulnerabilities. The generalizability of the system to other bug categories or more complex vulnerabilities is not sufficiently explored, which limits its applicability to different types of software projects.
While the paper reports false positives and true positives, there is insufficient discussion on the nature and causes of errors, especially false positives. A deeper analysis of why false positives occur and how they could be reduced or eliminated would improve the overall understanding of the limitations of REPOAUDIT.
Theoretical Claims: n/a
Experimental Designs Or Analyses: REPOAUDIT is both time-efficient and cost-effective. With an average analysis time of 0.44 hours per project and a low cost per bug detected, the system provides a practical and scalable solution for auditing large codebases. The comparison with traditional bug detection tools shows that REPOAUDIT is competitive, particularly in terms of precision and resource utilization.
REPOAUDIT’s performance is highly dependent on the underlying LLMs, particularly Claude 3.5 Sonnet, and the results may vary with other models. This reliance on a single model raises concerns about the system's robustness and adaptability across different LLMs or future updates. More discussion on the potential for model flexibility would strengthen the paper.
Supplementary Material: no Supplementary Material
Relation To Broader Scientific Literature: It utilizes a combination of parsing libraries, LLMs, and a multi-step exploration process to identify potential bugs within software repositories.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: see above
Other Comments Or Suggestions: n/a
Questions For Authors: see above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **1.Bug Customization**
Please refer to the response to the first concern **Bug Customization** of [Reviewer yKxy](https://openreview.net/forum?id=TXcifVbFpG¬eId=ZFh3alkmPr).
**2.Case Studies of FPs/FNs of RepoAudit**
Thank you for your suggestions. We collected the following typical cases and summarized the root causes of the FPs and FNs. We will add these cases and discussions to our revision.
**_Two False Positive Examples:_**
**Example 1:** In the project *icu*, the function `getTimeZoneRulesAfter` contains a `goto` statement making the control flow jump to the `error` label ([code](https://anonymous.4open.science/r/cases-BBFA/example1_1.md)). RepoAudit reports an FP of a Use-After-Free (UAF) at the second uprv\_free(newTimes) at line 13 due to the hallucination of Claude-3.5-Sonnet. The model incorrectly identifies a spurious program path that leads to uprv\_free(newTimes) after `newTimes` is freed in the loop.
**Example 2.** In the project `frr`, the function `vrf_get` can return NULL under certain conditions: In the function `lib_vrf_create` ([code](https://anonymous.4open.science/r/cases-BBFA/example2_2.md)), the return value of `vrf_get` ([code](https://anonymous.4open.science/r/cases-BBFA/example2_1.md)) is assigned to the pointer `vrfp`, which is subsequently dereferenced in the expression `vrfp->status` without a null check at line 13 in the function `lib_vrf_create`. RepoAudit reports it as a NPD, while it is an FP. Due to YANG schema validation, the `vrfname` variable is guaranteed to be non-NULL. Given that `vrf_get` only returns `NULL` when both `name == NULL` and `vrf_id == VRF_UNKNOWN`, it cannot return `NULL` when `vrfname != NULL`. Hence, the dereference is safe in practice. The root cause is that the LLMs are not aware of the fact that the return value of `yang_dnode_get_string` is never `NULL`.
**_A False Negative Example:_**
**Example 3:** In the `libsass` project, the function `sass_make_data_compiler` ([code](https://anonymous.4open.science/r/cases-BBFA/example3_1.md)) allocates a memory object and passes it as the second argument to `sass_prepare_context` ([code](https://anonymous.4open.science/r/cases-BBFA/example3_2.md)). Within `sass_prepare_context`, if `calloc` fails at line 3, `ctxmem` is set to 0, and the function returns 0 without freeing the allocated memory object `cpp_ctx` or assigning it to any other pointer, leading to a memory leak.
This bug was detected by Deepseek-R1 but missed by Claude-3.5 and GPT-4o Turbo. The latter models did not accurately track all relevant execution paths, particularly the error-handling path in this case. In contrast, reasoning-oriented models like Deepseek-R1 demonstrated superior capability in recognizing execution paths, allowing RepoAudit to detect such memory management issues more effectively.
**_Comparison with Existing Symbolic Tools:_**
Existing symbolic code auditing tools, such as Meta Infer, can avoid the FP and FN in Example 1 and Example 3, respectively, as they symbolically enumerate all the program paths, thereby covering the program behaviors along different paths. However, they are also unable to understand the behavior of `yang_dnode_get_string` as it depends on the library function `lyd_get_value`, of which the implementation is absent in the analyzed project. Therefore, existing symbolic tools can also report the FP in Example 2.
**_Future Improvements:_**
- **Enhancing Model Reasoning Capabilities**: We can improve the LLM’s ability to reason by either adopting more advanced models or fine-tuning the current models for specific tasks. Fine-tuning can be tailored to particular sub-tasks like exploring feasible program paths in single functions, thus mitigating the FPs and FNs (e.g., Examples 1 and 3). Additionally, incorporating specialized training datasets focused on code analysis could further enhance the model’s accuracy in these contexts.
- **Expanding the Tool Suite for Better Retrieval**: Another significant enhancement would involve integrating existing compilation-free analysis tools to identify all potential branches and loops within a program. This integration would offer a clearer representation of the program’s control flow structure to the model. Such an improved RAG design has the potential to significantly reduce the false positives and false negatives produced by RepoAudit, such as Examples 1 and 3.
- **Adding Multi-Modal Support for Library Function Understanding**: Utilizing library documentation and other non-code material as knowledge bases of the LLMs enables RepoAudit to understand library functions better. For example, the library documentation can facilitate RepoAudit in identifying the non-null value after YANG schema validation, thereby avoiding the FP in Example 2.
**3.Model Choice**
Please refer to the response to the first concern **Model Choice** of [Reviewer Le35](https://openreview.net/forum?id=TXcifVbFpG¬eId=5JaOhTUECl). | Summary: This paper proposes RepoAudit, an autonomous LLM-powered code auditing framework that can compete with current academic and industry solution tools. It consists of an initiator, an explorer, and a validator, working together to efficiently analyze GitHub repositories for code quality, security vulnerabilities, and compliance issues. Based on extensive experiments, it significantly addresses existing challenges, including the inability to analyze large repositories, high computational costs, excessive false positives, and the inefficiency of traditional static analysis methods.
Claims And Evidence: Yes, the claims are well supported by clear and convincing evidence.
Methods And Evaluation Criteria: The evaluatoin criteria make sense for the problem.
Theoretical Claims: There is no theoretical claims in the paper.
Experimental Designs Or Analyses: The experimental design and analysis are reasonable.
Supplementary Material: I reviewed the appendix to see more comparison results.
Relation To Broader Scientific Literature: This paper has a broad scientific impact on software engineering in the AI era, particularly in enhancing AI's ability to automatically detect potential bugs in large-scale repositories. It has strong practical significance.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: - I think fixing the base LLM to Claude makes the approach less general. The focus should be on the workflow rather than the inherent capabilities of the chosen LLM. Consider replacing the image that includes the Claude icon and restructuring the comparison of different LLMs in the main text instead of placing it in the appendix.
- I hope a clear table can be provided to compare current industry bug detectors and other LLM workflows, helping readers better understand the advantages of your approach.
Other Comments Or Suggestions: A clear process flow diagram of the RepoAudit framework is needed to illustrate its overall workflow and key components. Figure 3 should be enlarged and visually enhanced, positioned as the first image to provide readers with a concrete and direct understanding of the proposed workflow.
Questions For Authors: Is it possible to inject simple prompt manipulations into LLM-generated repositories to jailbreak RepoAudit and prevent it from reporting errors?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **1.Model Choice**
We evaluated RepoAudit using two additional LLMs, namely DeepSeek R1 and GPT-4 Turbo, which detected 44 and 14 true bugs with precisions of 75.86% and 35.90%, respectively. More detailed statistics of RepoAudit powered by DeepSeek R1 and GPT-4 Turbo were provided in Appendix C. During the author response stage, we further evaluated RepoAudit using two more LLMs, namely Claude-3.7 and GPT-o3-mini. By scanning the experimental subjects under the same settings, RepoAudit detected 40 and 36 true bugs with precisions of 78.43% and 76.60%, respectively.
As GPT-4 Turbo exhibits weaker code reasoning abilities than Claude-3.5-Sonnet and the reasoning models DeepSeek R1, Claude-3.7, and GPT-o3-mini, it would yield a weaker performance of RepoAudit. Notably, enhanced reasoning capabilities of stronger LLMs seamlessly benefit RepoAudit, demonstrating its great future potential. We will include further discussion on the performance of RepoAudit using different LLMs in the main body of the revision.
**2.Comparative Table with Existing Works**
We agree with your suggestion and will include the following comparative table in our revised manuscript, clearly contrasting RepoAudit against existing works:
| Name | LLM-based | Build-Free | Customizable | General Program | Repo-level |
|-------------------|-----------|------------|--------------|------------------|------------|
| GPTScan | Yes | Yes | No | No | No |
| LLMDFA | Yes | Yes | Yes | Yes | No |
| LLMSAN | Yes | Yes | Yes | Yes | No |
| Meta Infer | No | No | No | Yes | Yes |
| Amazon CodeGuru | No | Yes | No | Yes | Yes |
| **RepoAudit** | **Yes** | **Yes** | **Yes** | **Yes** | **Yes** |
As shown by the table, RepoAudit is the first work that supports the build-free and customizable analysis for repository-level bug detection upon general programs instead of domain-specific ones (e.g., smart contracts), supporting the security auditing of large-scale real-world software systems.
**3.Workflow Figure**
We will enhance the clarity and presentation of the workflow figure. Specifically, we will replace the Claude icon with a more proper icon and move the figure to page 2. Additionally, we will explicitly reference this improved diagram when describing our solution in the introduction, ensuring greater visual clarity and reader comprehension.
**4.Robustness to Prompt Manipulations**
Indeed, it is possible to inject (malicious) prompts into LLM-generated repositories, potentially causing RepoAudit to fail in bug detection. In the following code, we experimentally verified this by injecting several misleading natural language comments into the code. RepoAudit correctly identified a feasible buggy path and reported the confirmed bug in the original code version, but failed when analyzing the new version. Natural language comments in the code can significantly influence the inference results of LLMs, potentially misleading the model to incorrectly identify feasible paths as infeasible. An example is shown as follows:
In the project `memcached`, the function `proxy_init_startfiles` allocates a memory object and assigns it to the pointer `db`. Later, if `db->buf == NULL` or `db->fname == NULL`, the function returns without freeing the pointer `db`, causing a memory leak bug.
```
1 struct _mcp_luafile *db = calloc(sizeof(struct _mcp_luafile), 1);
2 if (db == NULL) {
3 fprintf(stderr, "ERROR: failed to allocate memory for db\n");
4 return -1;
5 }
6
7 db->buf = calloc(db->size, 1);
8 if (db->buf == NULL) {
9 /* inject point */
10 fprintf(stderr, "ERROR: failed to allocate memory for db->buf\n");
11 return -1;
12 }
13
14 db->fname = strdup(p);
15 if (db->fname == NULL) {
16 /* inject point */
17 fprintf(stderr, "ERROR: failed to allocate memory for db->fname\n");
18 return -1;
19 }
```
RepoAudit successfully identified this bug in the original version of the code. However, after adding the comment stating, **"This path will never be executed,"** at lines 9 and 16, RepoAudit failed to detect the bug. The key reason is that the comments mislead the LLMs to identify the buggy paths that pass the lines 9-11 and the lines 16-18 as infeasible.
Lastly, it is important to note that RepoAudit is designed as a developer-oriented code auditing tool. Our threat model assumes developers do not intentionally insert misleading content into their own codebases. Our evaluation effectively demonstrates RepoAudit's practical utility in real-world scenarios. While improving LLM robustness against prompt manipulations is crucial, this aspect is orthogonal to our current research focus and beyond the scope of this work. | Summary: This paper attempts to address a key concern in LLM-based code auditing systems where repositories are too complex and big to be effectively audited by LLMs. To address this, RepoAudit explores the repository on demand by analyzing data flow relations between different sections of the repository to build a more focused context for finding bugs. It also includes a validator to check satisfiability and reduce hallucination. Overall, it shows better performance than industry-standard auditing software.
Claims And Evidence: I believe the claims are clear and the evidence supports most of them. However in the introduction, one main limitation of existing systems is that using them to find new bugs requires a lot of expertise. The authors do not, to my knowledge, address this limitation in this paper. It would be nice to have a discussion about the effort required to use it in a custom repository to find bugs that may not be well known CWEs.
Methods And Evaluation Criteria: The paper presents a good evaluation, but I would have liked to see some more insights in general, especially with the error analysis of any false positives or negatives. For instance, were there any FPs/FNs that RepoAudit missed but were captured by the other baselines? Are there any common characteristics of the bugs missed by the tool? Despite the attempts to validate the results were there any cases which slipped through?
Theoretical Claims: Didn't verify.
Experimental Designs Or Analyses: I didn't verify the experiment results, but I believe the design is sound and the analysis makes sense. I would have appreciated more insights (mentioned earlier).
Is there a reason you did not include CodeQL as one of the baselines? It is not necessary, and suffers from much of the same issues as Infer, but it is quite popular, hence the question.
Supplementary Material: I reviewed the experiments in the supplementary material (Apps A, B).
Relation To Broader Scientific Literature: The field of bug-finding and code auditing is very actively researched, so I believe this paper is relevant to the broader scientific literature. Summarizing large data to fit the context of LLMs is a significant part of this, and using dataflow analyses to do so within repository-level code makes sense.
Essential References Not Discussed: Not that I know of.
Other Strengths And Weaknesses: I like the writing of the paper as well as the ideas presented. I personally don't see any other major weaknesses, apart from a lack of discussion on the effort required to reuse the same system for repositories written in different languages or for finding other kinds of bugs. Just a paragraph on generalizing across bugs, or coding languages (e.g. what would I need to do to use RepoAudit to find null pointer dereferences on a repository written in a different language). Actually I don't believe I saw any description of the programming language of the repositories being evaluated, so adding that is important.
Other Comments Or Suggestions: 1. Please add the number of FPs for RepoAudit in the intro, right now you only mention those for CodeGuru and Infer.
2. In section 2.2, I am unclear on what the hallucinations exhibited by the model are, and it is a bit tough to follow the explanation in Figure 2.
Questions For Authors: see above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **1.Customization and Expert Knowledge**
What we meant in the introduction section was that in order to detect a new type of bug, a new tool often needs to be developed inside some compiler, implementing bug-specific code checking rules. This often requires substantial compiler and program analysis expertise. With our design, extending RepoAudit to a new bug type may only entail providing a textual definition of the bug and few-shot examples (please also see our response to question 4 below). That said, the current implementation of RepoAudit focuses on bugs that are caused by data-flow, which covers a wide spectrum of bug types, such as SQL injection, Cross-site Scripting, and Absolute Path Traversal. Supporting bugs that do not entail data-flow, such as concurrency bugs, requires further development. We will clarify this in the revision.
**2.More Case Studies and Insights**
Please refer to the response to the second concern **Case Studies of FPs/FNs of RepoAudit** of [Reviewer HHzn](https://openreview.net/forum?id=TXcifVbFpG¬eId=enl0Gy3OnD).
**3.Comparison with CodeQL**
Initially, we considered using CodeQL as a baseline in our evaluation. However, upon investigation, we found that CodeQL lacks built-in detectors for the three bug types targeted by RepoAudit (i.e., NPD, MLK, and UAF). Therefore, we selected Meta Infer and Amazon CodeGuru as baselines, as both provide relevant built-in analyses for the targeted memory-related bugs. We will include more justification for our baseline selection criteria in the revision.
**4.Migration to Other Languages and Bug Types**
Our evaluation currently focuses on C/C++ programs, but RepoAudit actually supports three additional languages: Java, Python, and Go. Supporting a new language typically requires writing a few hundred lines of Python code to implement a few primitives needed by the auditing engine, such as the caller/callee retrievers and specific program value extractors using the *tree-sitter* parsing library. Although multilingual support is not our paper’s primary contribution, we will include additional discussion on this aspect in the revised evaluation section.
As we stated in our response to the first concern, RepoAudit supports various types of bugs—including those not associated with well-known CWE categories, such as domain-specific bug types. For example, in financial systems, there are often custom security policies such as *"user-sensitive data must not be logged in system outputs."* RepoAudit can handle such cases as long as the users define the form of sensitive data and logging operations as source and sink values, respectively, via several few-shot examples along with natural language descriptions. Moreover, this customization process is lightweight and incurs little manual effort. In our experiments, each bug type can be configured using no more than five few-shot examples, and the total number of words needed in the natural language prompt does not exceed 50 words.
We sincerely thank the reviewer for offering valuable suggestions. We will include a more detailed discussion on the migration to other languages and bug types in the revision. | Summary: The paper presents RepoAudit, an autonomous LLM-agent designed for repository-level code auditing. RepoAudit leverages large language models to find critical bugs such as null pointer dereference, memory leak, and use-after-free. The agent efficiently scans code repositories by utilizing an agent memory system that enables on-demand exploration of relevant functions. It mimics human code auditing by focusing on path-sensitive reasoning, making it scalable and adaptable to complex repositories. By addressing the challenges of context limits and hallucinations, the system provides significant improvements over previous methods, detecting 38 true bugs in 15 real-world systems with an average cost of $2.54 per project.
Claims And Evidence: 1. The paper states that REPOAUDIT overcomes intrinsic LLM limitations. Controlled experiments in Sections 2.2 and 2.3 provide qualitative evidence, however, the examples are narrowly scoped. It is not entirely convincing that these mitigations will hold up consistently across more complex codebases.
2. Fairness of performance claim is unclear; specifically, the issues with INFER (such as build errors or incompatibilities) might reflect implementation or integration challenges rather than fundamental performance differences in code auditing.
Methods And Evaluation Criteria: The methods and evaluation criteria are largely well-suited to the problem of repository-level code auditing.
Theoretical Claims: The paper relies on controlled experiments and qualitative demonstrations, such as the examples of pointer handling and feasible program path exploration in Figure 2, to substantiate their assertions about the limitations of LLMs and the benefits of their approach.
Experimental Designs Or Analyses: 1. The reported failures of tools like Meta INFER may, in part, stem from integration or configuration issues rather than intrinsic limitations. This could bias the comparative results.
2. The experiments rely on a specific configuration of Claude 3.5 Sonnet (with a fixed temperature of 0.0). As LLM behavior can be sensitive to prompting parameters, it remains to be seen how robust the approach is under different settings or with other models.
Supplementary Material: All parts of supplementary material are reviewed.
Relation To Broader Scientific Literature: REPOAUDIT advances code auditing by combining established static/pointer analysis and LLM-based code understanding. This hybrid approach improves scalability and precision for repository-level analysis, addressing long-standing limitations.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: ### Strengths
1. RepoAudit detects bugs with high precision (65.52%) and uncovers new bugs in addition to those reported by existing systems.
2. The agent’s ability to reason across different program paths, avoiding irrelevant ones, makes it effective in finding bugs like NPD, MLK, and UAF.
### Weaknesses
1. While the system mitigates hallucinations through validation, it still produces some false positives that need manual validation.
2. Though scalable, the system’s approach to managing large repositories could face performance issues with significantly larger systems or those with complex interdependencies across functions.
3. Ablation study on different prompt parameters and different LLMs.
Other Comments Or Suggestions: N/A
Questions For Authors: Please refer to weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **1.Effectiveness in mitigating LLM's intrinsic limitations**
Apart from the case studies in Sections 2.2 and 2.3, we evaluated RepoAudit-NoAbs that excludes program abstraction and pointer handling. The column **RepoAudit-NoAbs** in Table 5 demonstrates that this ablation decreases the number of TPs by 44.74% and increases FPs by 105%, causing precision to drop to 33.87%. Further details are available in Appendix B.3.
After the paper submission, we scanned 10 more GitHub projects, which averagely have 251K LoC and 8.8K stars, indicating their high complexity and popularity. In total, RepoAudit detected 186 true bugs with the precision of 85.71%. 80 and 95 bugs have been fixed and confirmed, respectively. We will add such results to the revision.
The above results strongly indicate that RepoAudit effectively mitigates the intrinsic limitations of LLMs in our context. We will change our claim from "addressing" to “mitigating” as we agree that there is still substantial room to improve.
**2.Performance of analyzing more complex codebases**
In our additional evaluation, the projects are 1.67 times the size of those in our original evaluation. Despite the increased size, RepoAudit maintained high precision (85.71%) and completed the analysis of each repository in 0.82 hours on average. This is 1.86 times the time cost of analyzing the original benchmarks. Hence, time costs are nearly linear with project sizes, showing the graceful scalability of RepoAudit.
**3.Comparison with Meta Infer**
Our work aims to enhance the applicability and usability of code auditing. Thus, our evaluation against Meta Infer was carefully designed to fairly reflect real-world contexts:
- Given our motivation, the applicability of code auditing tools is a critical focus. In practical scenarios, build errors and compatibility issues directly affect deployment feasibility. Therefore, beyond evaluating precision, recall, and efficiency, assessing a tool's practical applicability is crucial.
- The continuous evolution and variety of compilers and build systems render build-dependent tools like Meta Infer vulnerable to fundamental deployment issues—not merely integration or implementation challenges. Surveys by industry leaders highlight these fundamental obstacles [R1, R2], significantly hindering the broader deployment of the tools.
In our revision, we will justify the comparison setting and explain the real-world impact of build failures and incompatibilities.
> [R1] Why don't software developers use static analysis tools to find bugs? ICSE 2013
>
> [R2] Christakis M, Bird C. What developers want and need from program analysis: an empirical study. ASE 2016
**4.Performance with alternative LLMs**
Please refer to the response to the first concern **Model Choice** of [Reviewer Le35](https://openreview.net/forum?id=TXcifVbFpG¬eId=5JaOhTUECl).
**5.Performance using different temperatures**
Existing studies [R3, R4] on reasoning tasks suggest setting the temperature parameter to 0, thus reducing randomness in outcomes. Our work followed this practice. We will justify the setting in our revision.
During the author response stage, we further evaluated RepoAudit using Claude-3.5-Sonet under different temperatures. The results are as follows.
| Temp | #TP | #FP | #Reproduced | Precision (%) | Recall (%) |
|-------------|-----|-----|--------------|----------------|-------------|
| 0 | 38 | 20 | 21 | 65.52 | 100.00 |
| 0.25 | 33 | 20 | 20 | 62.26 | 95.24 |
| 0.5 | 36 | 23 | 21 | 61.02 | 100.00 |
| 0.75 | 35 | 20 | 18 | 63.64 | 85.71 |
| 1.0 | 33 | 24 | 18 | 57.89 | 85.71 |
RepoAudit remains robust across a range of temperature settings, with precision fluctuating slightly but remaining above 57%, and recall consistently high. Here, the precision is computed by #TP/(#TP + #FP), while the recall shows the proportion of reproduced bugs. We will incorporate these detailed findings and analyses into the revision.
> [R3] Satlm: Satisfiability-aided language models using declarative prompting, NeurIPS 2023
>
> [R4] SWE-bench: Can Language Models Resolve Real-world Github Issues? ICLR 2024
**6.Manual validation of false positives**
As shown by a large body of existing literature [R5], static code auditing inevitably produces false positives when detecting vulnerabilities in real-world scenarios. Manual post-validation thus remains a common practice. Notably, our evaluation shows RepoAudit surpasses the precision of SOTA industrial tools, indicating a reduction in required manual verification efforts compared to existing solutions. We will include the discussion regarding manual validation and its implications for using RepoAudit in our revision.
> [R5] Mitigating false positive static analysis warnings: Progress, challenges, and opportunities, TSE 2023 | null | null | null | null | null | null |
Distributionally Robust Policy Learning under Concept Drifts | Accept (poster) | Summary: This paper propose the distributionally robust method for offline bandit under concept shift, where the P(Y|X) is shifting. They propose a doubly robust method and DRO under KL divergence for offline policy learning. And they show the Asymptotic normality of the ope and propose a policy learning and the corresponding regret bound.
Claims And Evidence: 1) 'To be concrete, imagine that the distribution of covariates changes while that of Y | X remains invariant — in this case, the distribution shift is identifiable/estimable since the covariates are often accessible in the target environment. As a result, it is often unnecessary to account for the worst-case covariate shift rather than directly correcting for it.' This is not true, when there is some OOD data, especially in RL.
2) Comparing with [1], what is the other difference except for the doubly robust estimator and you are only considering the concept shift instead of the joint shift?
3) Is it possible that you provide some bias and variance of the proposed value estimator? And what is the benefit of Asymptotic normality, or in other word, why do we want this or what is the advantage compared with other estimator that is not Asymptotic normality?
[1] Si, N., Zhang, F., Zhou, Z., and Blanchet, J. Distributionally robust batch contextual bandits. Management Science, 2023.
Methods And Evaluation Criteria: Looks good to me.
Theoretical Claims: Yes. I check the proof of the regret bound.
Experimental Designs Or Analyses: Yes. I check the whole data generation process.
Supplementary Material: I only go through some of the proof of the lemma from the main text.
Relation To Broader Scientific Literature: Provide a reliable method for the policy learning under concept shift, which is crucial for domain adaptation under the concept.
Essential References Not Discussed: The following paper also discuss the DRO for policy learning, maybe you can also discuss in the related work.
[1] Distributionally Robust Policy Gradient for Offline Contextual Bandits
Other Strengths And Weaknesses: See above.
Other Comments Or Suggestions: Maybe highlight the difference of your method compared with [1].
Discuss (Hamming entropy integral) intuitively, currently it is hard to follow.
[1] Si, N., Zhang, F., Zhou, Z., and Blanchet, J. Distributionally robust batch contextual bandits. Management Science, 2023.
Questions For Authors: See above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for dedicating the time to review our paper and for providing the insightful comments. Due to the character limit, we cannot upload the revised manuscript, however we have edited according to the reviewer's helpful suggestions. Reference can be found in our reply to Reviewer wdwV.
Claims And Evidence
1 To our best knowledge, context shift and concept shift are two big sources of out of distribution data. In our setting, we are concerned with concept shift dataset, i.e. OOD data such that the distribution of $Y|X$ in testing data is shifted from that in training data. In the quoted sentence, we are discussing the other case of context shift, where the distribution of $X$ in testing data is shifted from that in training data, with the conditional reward $Y|X$ distribution unchanged. Please let us know if we have misunderstood your question.
In our revision, we have extended our framework to incorporate context shift. One can find that the policy value in this case is $\mathcal{V}\_{\delta}(\pi) = -\mathbb{E}\_{P}[r(X)(\alpha^*_\pi(X)e^{-\frac{Y(\pi(X))+\eta^*_\pi(X)}{\alpha^*_\pi(X)}-1}+\eta^*_\pi(X)+\alpha^*_\pi(X)\delta)]$, where $r(x)=\frac{P'_X}{P_X}$ with $P'_X$ being the shifted context distribution. Here, we make a conscious choice to estimate the context shift (as opposed to hedge again the worst-case shift) because in most practical situations, users have access to the covariates in the target environment and the context shift is identifiable and estimable; it is thus unnecessary to guard against the worst-case shift. We have added this extension to our manuscript.
2 Thank you for your question. The concept-shift setting is one of the major differences: we aim at providing a better solution to DRO policy learning when knowing additionally the **type** of distribution shift. Such a change of objective brings substantial technical challenges, which are what we have addressed in this paper.
Except for the differences in settings, [1] assumes a known behavior policy $\pi_0$ (and thus known propensity score), while our setting allows for an unknown $\pi_0$, which adds new challenge as slow estimation rates of the propensity score could result in high regret bound. We note that unknown $\pi_0$ setting is ubiquitous in observational studies [9]. This challenge calls for regression methods for fitting $\pi_0$ and an intricate design of empirical risk minimization (ERM) method, combined with a double-robust construction, in our work to compensate for the unknown $\pi_0$. In spite of all these challenges, we managed to show theoretically and empirically that, if only concept shift takes place, then employing [1] is suboptimal, and our algorithm does better with this one bit of extra information. We have added this comparison to our literature review section.
In terms of theoretical analysis, we adopt the chaining technique to achieve a regret rate of $O(n^{-1/2})$, while [1] uses a quantile trick.
3 Thank you for your question. To learn a near-optimal policy that maximizes the distributionally robust value $\mathcal{V}\_{\delta}(\pi)$ from a dataset, a consistent (i.e. asymptotically normal) estimator of $\mathcal{V}\_{\delta}(\pi)$ is a necessary intermediate step to achieve good quality learning. Asymptotic normality allows for inference on the policy value (e.g., constructing confidence intervals, conducting hypothesis testing). In terms of the variance of the proposed value estimator, asymptotically the variance is $\sigma_\pi^2$ as stated in Theorem 3.5. This is to say that the bias is asymptotically 0, given consistent nuisance parameter estimators. The non-asymptotical bias contributed by each nuisance parameter estimator is carefully analyzed in Appendix D.2, proof of Theorem 3.5.
Other Comments Or Suggestions
1 See Claims and Evidence 2
2 Hamming entropy integral is a variant of the classical entropy integral introduced in [10], based on the Hamming distance, which is a well-known metric for measuring the similarity between two equal-length arrays (policies in our context) whose elements are supported on on discrete sets. Hamming entropy integral is widely used in offline learning literature [1-4] for measuring the complexity of a policy class. Details and examples can be found in [1].
---
Rebuttal Comment 1.1:
Comment: Thanks for the effort in addressing my questions. I will raise my score to 3.
---
Reply to Comment 1.1.1:
Comment: Thank you so much for your time and positive feedback! | Summary: This paper investigates distributionally robust policy learning with concept shift. While this problem has been previously studied in the literature, the current work extends to a more general setting where the context space is not necessarily finite. To address this generalized setup, the authors propose a doubly robust estimator. The paper demonstrates that the policy value estimator exhibits asymptotic normality when the nuisance parameters are estimated with sufficient accuracy. Besides, other key contributions include establishing upper bounds for general spaces and providing corresponding lower bounds.
Claims And Evidence: I found the problem setup with exclusive focus on concept shift to be somewhat artificial. If there is only concept shift without uncertainty about the marginal distribution of the context $X$, it seems more natural to optimize the policy for each $X$ *individually*. Indeed, when $\Pi$ encompasses all possible policies (or rectangular in the sense that having separate constraints for each context), by the interchangeability principle, the optimal policy that solves equation (1) satisfies:
$$\pi^*(X) \in \arg\max_{p \in \Delta(A)} \inf_{Q_{Y|X} \in \mathcal{P}(P_{Y|X},\delta)} \mathbb{E}_{Y|X}[Y(p)|X],$$
where $\Delta(A)$ is the set of randomized actions.
The restriction to specific policy families in the paper typically serves the purpose of generalization—learning a policy that performs well across the entire context space. However, the concept-shift-only setup implies no need for such generalization since $P_X$ is assumed to be known exactly. While there might be practical applications requiring certain policy forms or impose constraints across different contexts, apparently the paper does not focus on these considerations. To me, the joint or separate uncertainty in both $P_X$ and $P_{Y|X}$ makes more sense to me.
Furthermore, given the assumption of no uncertainty in the marginal distribution of context $X$, one would expect generalization error bounds that are stronger than those presented in the paper, potentially avoiding the curse of dimensionality described at the end of Section 3.1. It's particularly concerning that Assumption 3.4 requires a dimension-independent convergence rate, which the results in Section 3.1 cannot achieve for high-dimensional spaces without imposing unrealistically strong smoothness constraints.
Methods And Evaluation Criteria: The numerical experiments would be substantially strengthened by including real-world datasets to demonstrate the effectiveness of the proposed method. Currently, the empirical validation appears limited to an artificial synthetic data, which may not fully capture the complexities encountered in practical applications. Having real data also helps solidify the concept-shift-only setup investigated in this paper.
Theoretical Claims: The results look reasonable to me and the proofs are quite standard, although I did not check every detail and I wonder if they are optimal or too conservative given that the context distribution is assumed to be known exactly.
Experimental Designs Or Analyses: As mentioned above, I think the experiments are too preliminary and it would be nicer to have real datasets support the assumed setup in the paper.
Supplementary Material: I went through them on a high level.
Relation To Broader Scientific Literature: In the literature, both joint and separate uncertainty in concept and covariate shift are studied. This paper focuses exclusively on the concept shift. It might have important applications and implications, but unfortunately the paper, in its current form, does not articulate it well.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: NA.
Other Comments Or Suggestions: None.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for dedicating the time to review our paper and for providing the insightful comments. Due to the character limit, we cannot upload the revised manuscript, however we have edited according to the reviewer's helpful suggestions. Reference can be found in our reply to Reviewer wdwV.
Claims and Evidence
1&2 We would like to first note that our work **does not assume known context distribution** $P_X$. We only assume that no covariate shift takes place (which has been relaxed in our revision), and we aim to learn an optimal policy that is robust to any shift of $P_{Y\mid X}$ within the $\delta$ KL-divergence. The setup is similar to the setting of [2], with the latter focusing on a finite covariate space.
We also note that the per-x optimization formulation proposed your comment 1 itself is **highly challenging when $X$ has continuous components and/or is high-dimensional** ---indeed, it then requires to evaluate $\mathbb{E}[Y | X=x]$ for each $x$. At a high level, this is the challenge our work addresses.
In our revision, we have extended our framework to incorporate context shift. One can find that the policy value in this case is $\mathcal{V}\_{\delta}(\pi) = -\mathbb{E}\_{P}[r(X)(\alpha^*_\pi(X)e^{-\frac{Y(\pi(X))+\eta^*_\pi(X)}{\alpha^*_\pi(X)}-1}+\eta^*_\pi(X)+\alpha^*_\pi(X)\delta)]$, where $r(x)=\frac{P'_X}{P_X}$ with $P'_X$ being the shifted context distribution. Here, we make a conscious choice to estimate the context shift (as opposed to hedge again the worst-case shift) because in most practical situations, users have access to the covariates in the target environment and the context shift is identifiable and estimable; it is thus unnecessary to guard against the worst-case shift. We have added this extension to our manuscript.
3 As discussed in our previous reply, we do not assuming knowing $P_X$ and solving the per-$x$ optimization problem is challenging with continuous and/or high-dimensional $X$---this is where the curse of dimensionality kicks in (think of the task of estimating conditional mean).
We also note that Assumption 3.4 is standard in offline learning literature [1,2,3,4,5]. The empirical sensitivity analysis of Assumption 3.4 can be found in [7] which justifies it. The results in [7] also parallels standard conditions in double-machine-learning, achievable by a variety of machine-learning methods [6].
Methods And Evaluation Criteria: We are now running a new set of experiments with real-world dataset, which will be ready before the camera ready version.
Theoretical Claims: The **optimality of our regret bound** is verified by our lower bound result of $\Omega(n^{-1/2})$ in Theorem 4.6. In terms of results in literature, our setting is similar to that of [2], however [2] only considers discrete $P_X$ with finite support, while we extend the case to continuous unknown $P_X$ with infinite support. We also improve the regret bound of in [2]. Please see table 1 for an overview of results in literature and our results.
Relation To Broader Scientific Literature: Concept shifts occurs in many real-world situations. For example, in advertising, the customer behavior can evolve over time as the environment changes, while the population remains largely the same. In personalized product recommendation, similar population segments in developed and emerging markets may prefer different product features.
Most existing robust policy learning algorithms model joint distributional shift without distinguishing the sources. The suboptimality of these algorithms under concept shift is because the worst-case distributions under the joint-shift model and the concept-drift model can be substantially different, so it would be a “waste” to consider joint shift under concept drift. With one extra bit of information, our work shows that we can obtain a better policy. The above discussion was already in our introduction, but we expanded it in our revision.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. I still have some concerns about the paper's setting that appear contradictory:
1. You mention the revision assumes that there is no context shift in $X$, yet at the same time, your response aims to address continuous and/or high-dimensional $X$ scenarios. Could you clarify whether different iid training and testing samples from the same underlying distribution are viewed as a type of distribution shift in your framework?
2. In the proposed way to handle context shift, the revision seems to require that the shifted distribution $P_{X'}$ is absolutely continuous with respect to $P_X$. This appears to be a strong assumption, especially for the continuous and/or high-dimensional $X$ emphasized in the response. And, how would you obtain $r(X)$?
3. The bound in Theorem 1 of [7] depends on the dimension $d$, and it only satisfies Assumption 3.4 when the sieve estimators meet specific smoothness requirements that may be too restrictive in high-dimensional settings.
I feel my main concerns haven't been adequately addressed. I will keep my score, but am open to further discussion.
---
Reply to Comment 1.1.1:
Comment: We would like to thank the reviewer for the timely responses and questions.
1 We are not sure if there is any misunderstanding, but we see **no contradiction** between "no distributional shift in $P_X$" and "continuous and/or high-dimensional context $X$ scenario". This just means that the distribution $P_X$ (which can be continuous and/or high-dimensional) that generates the training contexts and the testing contexts is the same. The challenges that comes from the continuity and the high-dimensionality of $X$ is orthogonal to context shift.
To avoid any further confusion, please allow us to reiterate our problem setting. We aim to learn a concept shift robust policy from a training dataset $\mathcal{D}=\{(X\_i,A\_i,Y\_i)\}\_{i=1}^n$ consisting of iid samples. The context (could be continuous and/or high-dimensional) $X_i\sim P_X$, the actions $A_i\sim\pi_0(X_i)$ conditioned on the context $X_i$, and the outcome $Y_i\sim P\_{Y(A\_i)|X_i}$ is sampled from a distribution supported on $\mathbb{R}$, conditioned on the context $X_i$ and the action $A_i$. The optimal policy $\pi^*$ is robust to any kinds of concept shift, which is to say it gains the highest outcome in expectation over any testing sample path $\mathcal{D}'=\{(X'\_i,\pi^*(X'\_i),Y'\_i)\}\_{i=1}^n$, where contexts $X'\_i\sim P\_X$ (**a different sample path from $(X\_i)_{i=1}^n$ in $\mathcal{D}$, but their underlying distribution $P_X$ is the same**), actions $\pi^*(X'\_i)$ are taken by the policy $\pi^*$ conditioned on the context $X'_i$, and outcomes are sampled from a shifted distribution $Y'\_i\sim P'\_{Y(\pi(X\_i))|X\_i}$, such that the KL-divergence between $P\_{Y(a)|X\_i}$ and $P\_{Y'(a)|X\_i}$ is within $\delta$ for any action $a$ in the action set. This is the standard problem setting in offline distributional robust optimization literature [1-5].
Our revision includes the extension of context shift, which has the same problem setup as above, except that now $P\_X$ in the training dataset is shifted to $P'\_X$ in the testing dataset and $P\_{Y(a)\mid X}$ does not shift. As before, the context $X$ can be continuous and/or high-dimensional.
To conclude, we studied the offline concept shift robust learning problem and in our revision, we also add the extension of context shift robust learning under estimable likelihood ratio.
2 Absolute continuity is required for all kinds of widely used $f$-divergences, including KL-divergence, Chi-squared divergence, and total variation distance. These divergences are well-studied in offline distributional robust optimization literature [1-5], even under continuous and/or high-dimensional $X$ [1,3-5], and as a result, absolute continuity has been assumed therein. We would like to politely point out that this is a strong assumption considering the literature. On the contrary, it is a standard assumption to define the distributional shift robust learning problem [1-5].
For learning $r(x)$, we note that by definition $r(x)=\frac{dP'_X}{dP_X}(x)$, where $\frac{dP'}{dP}$ is Radon-Nikodym derivative. As discussed before, since the context shift is often identifiable (i.e. we have access to context samples before and after the distributional shift, which are empirical realizations of $P_X,P'_X$ respectively), we can use regression techniques in our manuscript to fit $r(x)$, similar to the estimation of the propensity score $\pi_0(x)$. We also note that we have derived double robustness results in the presence of context shift.
3 We agree that the convergence rate depends on the dimension $d$, but such difficulties induced by high dimensionality are intrinsic for estimating and/or learning with conditional mean functions in nonparametric statistics. Note that the previous work [2] only considers $X$ with **a finite support**.
We would like to learn about references overcoming this issue if you can kindly point out them. | Summary: This paper develops a distributionally robust policy learning framework under concept drift by focusing on shifts in conditional reward distributions while assuming stable covariate distributions. It introduces a doubly robust estimator with root‑n convergence for policy evaluation and proposes an efficient policy learning algorithm with optimal regret bounds.
Claims And Evidence: The paper supports its claims through rigorous theoretical proofs (e.g., asymptotic normality and regret bounds) and empirical studies comparing with benchmark methods. However, some claims rely on strong assumptions for nuisance parameter estimation, which might require additional discussion.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are well-tailored to the problem of concept drift. The separation of conditional reward shifts from joint distribution shifts is well motivated, and the use of simulated experiments with cross-fitting provides a reasonable evaluation framework.
Theoretical Claims: I reviewed the proofs for asymptotic normality and the regret upper/lower bounds. They appear methodologically sound.
Experimental Designs Or Analyses: The experimental design is robust, featuring multiple data splits, cross-validation, and a clear comparison against an established benchmark. However, the reliance on simulated data and sensitivity to hyperparameters may limit insights into performance on real-world datasets.
Supplementary Material: I examined the proofs provided in Appendix D.1 (for strong duality), D.2 (for asymptotic normality of the policy value estimator), and D.4 (for the regret lower bound).
Relation To Broader Scientific Literature: The key contributions relate closely to recent advances in distributionally robust optimization and double machine learning. The work refines prior approaches—such as those by Si et al. (2023) and Mu et al. (2022)—by targeting concept drift specifically.
Essential References Not Discussed: While the paper cites relevant studies, it could benefit from discussing additional works on robust inference under distribution shifts, particularly recent advances in DRO and robust causal inference that address similar issues in a broader context.
Other Strengths And Weaknesses: Strengths:
1. Provides a clear theoretical framework with rigorous proofs and optimal regret bounds.
2. Effectively integrates doubly robust estimation with de-biasing and cross-fitting techniques.
3. Presents a well-structured algorithm and detailed explanation of the methodological steps.
Weaknesses:
1. Relies on strong assumptions for nuisance parameter estimation rates without extensive empirical sensitivity analysis.
2. Some derivations, especially in the ERM formulation, lack complete justification.
3. Limited discussion of potential drawbacks or failure cases in the simulation setup.
Other Comments Or Suggestions: 1. Clarify the presentation of cross-fitting steps and the functions involved in de-biasing, as some parts could benefit from more detailed explanations.
2.Provide additional details on hyperparameter selection in the simulation studies and discuss potential impacts of different settings.
3.A brief discussion on how the methodology might generalize to real-world data or continuous action spaces would enhance the paper's practical insights.
Questions For Authors: 1. What is the effect on the overall estimation error when nuisance parameter estimators converge slower than the required rate?
2. Can the proposed ERM and de-biasing approach be efficiently extended to handle continuous action spaces?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for dedicating the time to review our paper and for providing the insightful comments. Due to the character limit, we cannot upload the revised manuscript, but we have edited according to the reviewer's helpful suggestions. We use the following references.
[1] Si, N., Zhang, F., Zhou, Z., and Blanchet, J. Distributionally robust batch contextual bandits. Management Science, 2023.
[2] Mu, T., Chandak, Y., Hashimoto, T. B., and Brunskill, E. Factored dro: Factored distributionally robust policies for contextual bandits. Advances in Neural Information Processing Systems, 35:8318–8331, 2022.
[3] Athey, S. and Wager, S. Policy learning with observational data. Econometrica, 89(1):133–161, 2021.
[4] Zhou, Z., Athey, S., and Wager, S. Offline multi-action policy learning: Generalization and optimization. Opera- tions Research, 71(1):148–183, 2023.
[5] Kallus, N., Mao, X., and Uehara, M. Localized debiased machine learning: Efficient inference on quantile treatment effects and beyond. arXiv preprint arXiv:1912.12945, 2019.
[6] Victor Chernozhukov, Denis Chetverikov, Mert Demirer, Esther Duflo, Christian Hansen, Whitney Newey, and James Robins. 2018. Double/debiased machine learning for treatment and structural parameters. Econometrics Journal 21, 1 (2018), C1–C68.
[7] Jin, Ying, Zhimei Ren, and Zhengyuan Zhou. "Sensitivity analysis under the f-sensitivity models: a distributional robustness perspective." arXiv preprint arXiv:2203.04373 (2022).
[8] Kallus, Nathan, and Angela Zhou. "Policy evaluation and optimization with continuous treatments." International conference on artificial intelligence and statistics. PMLR, 2018.
[9] Rosenbaum, P.R. (2002). Observational Studies. Springer Series in Statistics. Springer, New York, NY.
[10] Dudley, Richard M. "The sizes of compact subsets of Hilbert space and continuity of Gaussian processes." Journal of Functional Analysis 1.3 (1967): 290-330.
Weakness
1 See Question 1
2 Thank you for your helpful comments. The ERM step follows from standard duality results in the DRO literature. To improve readability, we have added a detailed explanation of the ERM derivation in our manuscript. With an empirical dataset, it is natural to propose an ERM solution based on the loss function inspired by the strong duality result in Lemma 2.3.
3 A potential drawbacks in our framework (as well as in other distributional robust optimization works) is the choice of $\delta$. The parameter $\delta$ controls the size of the uncertainty set considered and thus controls the degree of robustness in our model --- the larger $\delta$, the more robust the output. The empirical performance of the algorithm substantially depends on the selection of $\delta$. A small $\delta$ leads to negligible robustification effect and the algorithm would learn an over-aggressive policy; a large $\delta$ tends to yield more conservative results. A more detailed discussion can be found in [1]. We have incorporated the above in the revision.
Comments and Suggestions
1 In terms of cross-fitting and de-biasing technique, we have added more detailed explanation in our manuscript.
2 In our simulation, we set $K=3$, which is the minimal number of splits possible, and the default spline threshold at 0.001 without fine-tuning. Under this default choice, we see that the algorithm already performs well. Increasing $K$ and decreasing the spline threshold would increase the computation complexity.
3 In real-world applications, knowing the **source** of the distribution shift effectively shrinks the uncertainty set, thereby yielding less conservative results (compared with the joint modeling approach). Moreover, since in most cases, practitioners have access to the covariate in target environment, it is then possible to identify and estimate covariate shifts: when the decision maker observes none or little covariate shifts and would like to hedge against the risk of concept drift, it is suitable to apply our method which outperforms existing method designed for learning under joint distributional shifts. We are now applying our method to a real dataset, which would be ready before camera ready version.
See Question 2 for generalization to continuous action space.
Questions
1 The rate Assumption 3.4 is standard in literature [1,2,3,4,5]: it suffices to have $o_P(n^{-1/4})$-rates on all nuisance parameters or no rate on $\hat{g}_\pi$ at all if $\pi_0$ is given. This assumption also parallels standard conditions in double-machine-learning, achievable by a variety of machine-learning methods [6]. The empirical sensitivity analysis can be found in [7] which justifies Assumption 3.4. We have added this discussion to our manuscript.
2 We agree with the reviewer that it might be possible to apply our ERM approach to the continuous action space extension, however the problem setting would deviate from the current discrete case, as discussed in [8]. We leave this for future works.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. My questions have been addressed.
---
Reply to Comment 1.1.1:
Comment: Thank you so much for your time and positive feedback! | null | null | null | null | null | null | null | null |
Mind the Gap: A Practical Attack on GGUF Quantization | Accept (poster) | Summary: The paper investigates the question of whether the quantization error in an LLM can be exploited towards practical attacks, that can lead the model to output maliciously on specific inputs, while not dropping significantly on standard benchmarks.
While this fact has been shown before by Egashira et al. (NeurIPS 2024) for simpler non-calibration quantization schemes, the present submission does this for the more modern and accurate "GGUF" format, which entails calibration. Thus, the submission shows that such models (which are extremely popular on repositories such as HuggingFace) could be practically exploited.
Claims And Evidence: The specific technical claims in the submission are sound and are supported by practical evidence. I will say though that the abstract claims are more generic than what is supported later in the paper. Specifically, the main abstract claim:
"Our key insight is that the quantization error – the difference between the full-precision weights and their (de-)quantized version – pro- vides sufficient flexibility to construct malicious quantized models that appear benign in full precision." is something that was first achieved by prior work for a simpler family of quantization schemes. The present work is the first one to do this for GGUF.
Methods And Evaluation Criteria: There is no standard benchmark for such methods, but the proposed evaluation criteria make sense.
Theoretical Claims: There are no real theoretical claims, the paper presents a heuristic.
Experimental Designs Or Analyses: The experimental design is valid (in fact, it is largely adapted from Egashira et al., which is already published work.
Supplementary Material: I have skimmed the supplementary material, in particular the detailed derivations of the heuristic and the details corresponding to the GGUF algorithm.
Relation To Broader Scientific Literature: The paper can be seen as a technical-report-style extension of the work of Egashira et al., in particular extending their approach to a more popular format.
Essential References Not Discussed: I think the related work coverage is fine.
Other Strengths And Weaknesses: Strenghts:
I think the paper proposes a valid extension of the work on attacks towards quantization methods, specifically since the format they are focusing on is probably the dominant one for local deployment of ML models. The heuristic approach proposed is well-justified, and well-supported through experiments.
Weaknesses:
Essentially, the work is at the level of a well-executed technical report, as it heavily builds on prior work, notably Egashira et al's paper in NeurIPS. As such, the work is of interest, but only to a relatively small niche in the community. The heuristic proposed is quite specialized to the (specialized) format considered, and I don't see how this would be extensible beyond the problem considered here. The defenses considered are largely the same as Shu et al. 2023.
Other Comments Or Suggestions: The paper is well-written and easy to follow.
Questions For Authors: I do not have any major questions, but I am curious if:
1. The authors looked into other approaches (e.g., specialized signatures?) for defending against such attacks?
2. Do the authors have some intuition towards more general results showing that any quantized format would be to some extent vulnerable to exploits on an unknown slice of inputs?
## post-rebuttal comment
I thank the authors for their responses. As stated before, I remain borderline on this paper (due to concerns outlined before), but will definitely not stand in the way of acceptance.
Ethical Review Concerns: No concerns.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: First, we would like to thank the reviewer for their efforts spent reviewing our paper, understanding the strength of our work, and providing many insightful comments. We address the reviewer’s questions and comments below.
**Q1: Is the claim in the abstract, *“Our key insight is that the quantization error … provides sufficient flexibility to construct malicious quantized models that appear benign in full precision”* aligned with the actual contribution of the paper?**
Yes. Although quantization is known to be susceptible to similar attacks, existing attacks are against rounding-based quantizations, and they rely on an analytical bound within which quantization results remain unchanged. In contrast, we are the first to show that the *quantization error itself* is exploitable against GGUF, where such an analytical bound cannot be calculated.
**Q2: Is the scope of the work wide enough and of interest to a broad community?**
Yes. As model sizes continue to grow, quantization techniques are becoming increasingly widespread, making research on their security highly practical and valuable. We are the first to reveal that GGUF, arguably the most widely used algorithm, is indeed susceptible to attacks. This demonstrates that a type of attack previously considered more a theoretical concern in the context of simpler quantization schemes, has now become a strong and practical threat. This, as unanimously acknowledged by other reviewers, has a significant impact, extending far beyond what we would consider a “small niche community” (GGUF quantized models have multiple hundreds of millions of downloads [1] with over 77.3k stars on llama.cpp, 135k on ollama, and 100+ apps building on it. Further, there are over 90k GGUF-quantized models on Hugging Face).
**Q3: Can the attack be extended to other quantization algorithms?**
[The reviewer dpB2 raised a similar point, so we repeat our unified response here.]
First, we would like to emphasize that, considering the overwhelming number of GGUF-quantized models and their users, demonstrating that our approach (error-based interval and heuristic expansion) successfully attacks *every variant of k-quant algorithms* of GGUF already provides substantial impact.
Still, as we acknowledge the importance of the extensibility of our approach, we conduct an additional experiment, targeting GPTQ (data-dependent) and HQQ (data-independent), which are both integrated into Hugging Face, we obtained the following results:
**===Vulnerable Conde Generation===**
| Model | Target Quantization | Security (Full) | Security (Quantized) | Utility (Full, HumanEval) |
| - | - | - | - | - |
| Qwen2.5-1.5b | GGUF, Q4_K_M | 89.2 | 12.5 | 41.4 |
| | GPTQ, 4bit | 96.0 | 42.6 | 40.9 |
| | HQQ, 4bit | 88.4 | 13.0 | 41.7 |
**===Content Injection===**
| Model | Target Quantization | ASR (Full) | ASR (Quantized) | Utility (Full, MMLU) |
| - | - | - | - | - |
| Qwen2.5-1.5b | GGUF, Q4_K_M | 0.3 | 40.2 | 59.8 |
| | GPTQ, 4bit | 0.5 | 1.1 | 59.3 |
| | HQQ, 4bit | 0.1 | 1.3 | 59.7 |
As these results indicate, our method partially extends to GPTQ / HQQ, even without being explicitly modified for them. Although the success rates of the attack are generally smaller than on GGUF, we consider this a promising result, with pushing the score further being an interesting avenue for future work to explore.
We thank the reviewer for raising an interesting direction for the discussion. We will include the results in the next revision.
**Q4: Can you elaborate why only Gaussian noise is used as a defense?**
[The reviewer dpB2 raised a similar point, so we repeat our unified response here.]
Certainly. We would like to clarify the following points: (i) Since our work focuses on the attack side, we believe that a rigorous investigation of defenses (including, e.g., other downstream effects of such defenses) is better suited for future work. (ii) Importantly, as there is so far no established defense in practice, the success of our attack without defending protocol already highlights a significant real-world threat. (iii) In order to acknowledge the importance of such defenses, we focused on a straightforward, easily applicable, and discussable approach, noising. While we do not extensively focus on defensive aspects, we note that our work provides some novel insights not discussed in prior research, such as the potential for model-specific optimized noise (regardless of the quantization type) to mitigate the attack.
**References**
[1] https://ollama.com/search
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their response. I continue to believe that the paper's contribution is too narrow, and that it is too close to the work of Shu et al. However, I will not stand in the way of acceptance, so I will upgrade my score by one point.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for the response and for updating their score. We highly appreciate the reviewer’s understanding of other views on our paper’s contributions, and would only like to briefly clarify their remaining point of criticism.
Based on the reviewer’s mention of “defenses considered are largely the same as **Shu et al.**” and the overall review content, we believe the reviewer’s reference to Shu et al. (On the Exploitability of Instruction Tuning) may have been intended to refer to Ma et al. (Quantization Backdoors to Deep Learning Commercial Frameworks) instead. If so, we believe to have already addressed the related points in our rebuttal, and to summarize:
(i) Our work targets GGUF, a fundamentally different quantization method from those studied in Ma et al. and Egashira et al. In fact, this is the first attack on popular optimization-based quantization.
(ii) The defense we study against our attack overlaps with that of Ma et al. by design—we aim to confirm that Gaussian noising still works. We will clarify this in the next revision of the paper. | Summary: This paper introduces a novel practical attack on GGUF quantization. It exploits the quantisation errors inherent in GGUF to hide malicious behavior into quantised models. The malicious behaviour of the model remains hidden in full precision but is revealed when the model is quantised.
Claims And Evidence: The claims are well-supported.
1. The attack is indeed novel.
2. The practicality of error-based interval estimation. Empirically validated.
3. Effectiveness across models and configs. Experimental evidence (e.g., increase in insecure code generation).
Methods And Evaluation Criteria: The proposed method is intuitively sound. The evaluations are practical and realistic. The threat model is sound.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experimental design is thorough. The authors use different LLMs, various quantisation types, and examine multiple attack scenarios.
Supplementary Material: -
Relation To Broader Scientific Literature: -
Essential References Not Discussed: -
Other Strengths And Weaknesses: -
Other Comments Or Suggestions: -
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their acknowledgement of the strength of our work. In case the reviewer has any other questions or comments, we are happy to engage in further discussion. | Summary: This paper presents a adversarial attack on GGUF quantization, a popular post-training quantization (PTQ) method in LLM. The core contribution is an error-based interval estimation technique, which exploits quantization errors to enable adversarial attack on LLMs. The authors demonstrate the attack's effectiveness across insecure code generation, targeted content injection, and benign instruction refusal. The authors also propose a heuristic interval expansion to simultaneously attack multiple quantization schemes. Finally, the paper discusses defenses such as Gaussian noise injection, in order to mitigate the attack.
Claims And Evidence: The claims are well-supported by clear and convincing evidence.
Methods And Evaluation Criteria: - The methodology is well-founded, leveraging quantization error analysis to construct adversarial attack.
- Experiments cover multiple LLMs, across different GGUF quantization types.
Theoretical Claims: The paper includes Theorem B.1 (Appendix B.3), proving that the interval-widening heuristic is upper-bounded for zero-shot quantization but I have not verified the proofs.
Experimental Designs Or Analyses: - Experiments are well-structured, covering a variety of quantization types and LLMs.
- The Gaussian noise defense experiment (Figure 4) is valuable, demonstrating a practical countermeasure.
Supplementary Material: I have not reviewed the supplementary material.
Relation To Broader Scientific Literature: - Builds on Egashira et al. (2024), extending adversarial quantization attacks to optimization-based quantization.
- Discusses similarities to data poisoning attacks (Carlini et al., 2023; Shu et al., 2023) but highlights that quantization-based attacks require no trigger tokens.
Essential References Not Discussed: None.
Other Strengths And Weaknesses: Strengths:
- New attack on GGUF quantization, a widely used PTQ technique in open-source LLM deployment.
- Strong experimental validation across multiple models, quantization types, and adversarial scenarios.
- Practical implications: Highlights real security risks in popular frameworks (llama.cpp, ollama).
- Well-written with clear problem motivation, methodology, and evaluation.
Weaknesses:
- The attack assumes the adversary knows the quantization method, which may not always be true in practice.
- More discussion on defenses (e.g., QAT-based robustness, adversarial training) would strengthen the paper.
- Limited discussion of practical defenses beyond Gaussian noise.
Other Comments Or Suggestions: Please address weaknesses above.
Questions For Authors: - What computational resources are required for the attack, and is it feasible for an adversary with limited resources?
- Can the attack generalize to other optimization-based quantization methods beyond GGUF k-quants?
- Beyond Gaussian noise, what other defenses were considered, and why were they not explored further?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the efforts spent reviewing our paper and the positive assessment. We address the reviewer’s questions and comments below.
**Q1: Can you elaborate on whether it is reasonable to assume that the adversary has access to the quantization algorithm?**
Certainly. We agree with the reviewer that this is an important aspect of our attack setting. Notably, in practice, we find that many widely used quantization schemes are open and fully accessible, particularly as a primary use case for local model deployment on commodity hardware. This level of accessibility goes hand-in-hand with the popularity of such schemes and makes them a primary target for adversaries who aim at potential real-world impact.
The focus of this work perfectly exemplifies this, as the GGUF algorithm is both open-source / publicly available [1] and widely used with hundreds of millions of model downloads. Therefore attacking GGUF (knowing the algorithm) is a realistic and practical threat model with significant real-world implications. Here, we additionally note that many of our attacks target multiple schemes (variants) simultaneously, broadening the attack surface as the applied variant only has to be included in the adversary's target set.
In a similar spirit, many other popular algorithms are also open-sourced, including LLM.int8() / NF4 / FP4 [2], which are already known to be vulnerable to similar attacks, alongside other well-known algorithms [3-5] which therefore constitute interesting avenues for future work.
**Q2: Can the authors elaborate on why they did not investigate further defenses?**
[The reviewer BR9t raised a similar point, so we repeat our unified response here.]
Certainly. We would like to clarify the following points: (i) Since our work focuses on the attack side, we believe that a rigorous investigation of defenses (including, e.g., other downstream effects of such defenses) is better suited for future work. (ii) Importantly, as there is so far no established defense in practice, the success of our attack without a defense protocol already highlights an immediate significant real-world threat. (iii) In order to acknowledge the importance of such defenses, we focused on a straightforward, easily applicable, and discussable approach, noising. While we do not extensively focus on defensive aspects, we note that our work provides some novel insights not discussed in prior research, such as the potential for model-optimized noise (regardless of the quantization type) to mitigate the attack.
**Q3: How much compute is required for the attack?**
The attack requires roughly the same amount of GPUs as required for typical (full) fine-tuning. For training Llama 3.1-8B in our main result, 2 x 80 GB GPUs (for 8 hours, this amounts to roughly $50) are required, which we believe is feasible in practice.
**Q4: Can the attack be extended to other quantization algorithms?**
[The reviewer BR9t raised a similar point, so we repeat our unified response here]
First, we would like to emphasize that, considering the overwhelming number of GGUF-quantized models and their users, demonstrating that our approach (error-based interval and heuristic expansion) successfully attacks *every variant of k-quant algorithms* of GGUF already provides substantial impact.
Based on the reviewer's comments and acknowledging the importance of the extensibility of our approach, we conduct an additional experiment, targeting GPTQ (data-dependent) and HQQ (data-independent), which are both integrated into Hugging Face:
**===Vulnerable Conde Generation===**
| Model | Target Quantization | Security (Full) | Security (Quantized) | Utility (Full, HumanEval) |
| - | - | - | - | - |
| Qwen2.5-1.5b | GGUF, Q4_K_M | 89.2 | 12.5 | 41.4 |
| | GPTQ, 4bit | 96.0 | 42.6 | 40.9 |
| | HQQ, 4bit | 88.4 | 13.0 | 41.7 |
**===Content Injection===**
| Model | Target Quantization | ASR (Full) | ASR (Quantized) | Utility (Full, MMLU) |
| - | - | - | - | - |
| Qwen2.5-1.5b | GGUF, Q4_K_M | 0.3 | 40.2 | 59.8 |
| | GPTQ, 4bit | 0.5 | 1.1 | 59.3 |
| | HQQ, 4bit | 0.1 | 1.3 | 59.7 |
As these results indicate, our method partially extends to GPTQ / HQQ, even without being explicitly modified for them. Although the success rates of the attack are generally smaller than on GGUF, we consider this a promising result, with pushing the score further being an interesting avenue for future work.
We once again thank the reviewer for raising an interesting direction for the discussion. We will include the results in the updated paper.
**References**
[1] https://github.com/ggml-org/llama.cpp
[2] https://github.com/bitsandbytes-foundation/bitsandbytes
[3] https://github.com/ModelCloud/GPTQModel
[4] https://github.com/mit-han-lab/llm-awq
[5] https://github.com/Vahe1994/AQLM
---
Rebuttal Comment 1.1:
Comment: Thanks for addressing my concerns and I am happy to stick my current rating of "Weak accept".
---
Reply to Comment 1.1.1:
Comment: We are glad to learn that we could address the reviewer's concerns and thank them for confirming their already positive score. | Summary: This paper introduces a backdoor attack targeting GGUF quantization, a widely used optimization-based post-training quantization method for LLMs. The paper proposes an error-based interval approach to construct malicious quantized models that behave normally in full precision but exhibit targeted malicious behaviors, targeting insecure code generation, content injection, and refusal of benign instructions when quantized using various GGUF k-quant types. The attack leverages the quantization error to derive constraints during adversarial fine-tuning, aiming to maintain the malicious behavior after quantization while hiding it in the full-precision model. The paper demonstrates the attack's effectiveness on multiple LLMs and quantization types.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/a
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: Note that quantisation backdoor attacks are not particularly new as a setting -- there were earlier papers eg Ma et al. Paper at hand demonstrates that widely used quantisation schemes are similarly vulnerable, even for more complex LLM tasks. I think the paper in its current form ignores quite a lot of literature in backdoor attack broadly (e.g. compiler-based injections of Clifford et al., handcrafted backdoors of different kind e.g. Carlini et al., architectural e.g. from Langford et al. ), and does not compare explicitly to old literature on quantisation backdoors more specifically.
Essential References Not Discussed: I would expand the related work quite a bit to cover other backdoor attacks and provide an explicit scenario in which such attack can take place, maybe placing it within framework of Clifford et al. (https://ieeexplore.ieee.org/document/10516650).
Other Strengths And Weaknesses: Very nicely written work
Other Comments Or Suggestions: - Thanks for adding the requested comparison
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: First, we thank the reviewer for the time spent reviewing our paper and the positive assessment. We address the reviewer’s questions and comments below.
**Q1: Can you please extend and reframe the literature review about the backdoor attack?**
Certainly. We acknowledge the importance of covering backdoor attacks more widely and will add the suggested references and reformulate relevant literature sections in the next revision. In the formulation of Clifford et al. [1], our threat model is largely aligned with the existing quantization attack by Ma et al. [2]: our attack can be achieved if the adversary can “train” a model using a malicious “dataset”. However, our work is different in that existing quantization backdoors have so far only been proposed for simpler rounding-based algorithms, while we are the first to attack a more widely used and complex optimization-based algorithm, GGUF.
**Q2: Can the authors compare their work with old quantization attacks more explicitly?**
Absolutely. We conducted the experiments by targeting GGUF with the method used by Ma et al. [2] and Egashira et al. [3]. We obtained the following result for Qwen2.5-1.5b with the Content Injection setting:
| Method | Full Precision ASR | Quantized ASR |
| - | - | - |
| Our method | 0.2 | 50.1 |
| Method in [2-3] | 0.1 | 0.1 |
As shown above, the older method fails to achieve any contrast between full precision and quantized models. We note that as GGUF is optimization-based and scaling is determined by considering all parameters within a block, fundamental assumptions of prior attacks (i.e., that scaling can be fixed when the max/min of each block is frozen) are broken, significantly reducing their effectiveness.
We thank the reviewer for raising an important direction to improve our work; we will add it in the next revision of our paper.
**References**
[1] Clifford et al., ImpNet: Imperceptible and blackbox-undetectable backdoors in compiled neural networks, IEEE SaTML 2024.
[2] Ma et al., Quantization Backdoors to Deep Learning Commercial Frameworks, IEEE TDSC 2023.
[3] Egashira et al., Exploiting LLM Quantization, NeurIPS 2024. | null | null | null | null | null | null |
Federated In-Context Learning: Iterative Refinement for Improved Answer Quality | Accept (poster) | Summary: This paper proposes the Fed-ICL framework to harness the benefits of ICL while ensuring privacy preservation in sensitive settings, which is the first framework of iterative optimization of federated learning (FL) with a parameter-free communication scheme to enable iterative refinement of responses. The authors establish a theoretical foundation for Fed-ICL by analyzing its performance on a simplified single-layer Transformer model and conduct extensive experiments across a diverse set of QA tasks, which show their framework's effectiveness.
Claims And Evidence: The evidence is convincing in general, but I think it might be better to show their framework's robustness to privacy attacks since they mention that they combine the efficiency property of ICL and the privacy robustness of FL.
Methods And Evaluation Criteria: The ablation study and the comparison with other methods on different datasets are comprehensive. One of my suggestion is the same as the previous section to prove the privacy ability somehow. Also, since these 2 datasets are in the area of QA, but right now more and more people care about the reasoning ability of LLMs, I wonder if this pipeline can still be effective in the reasoning tasks, which may make this work more impactful.
Theoretical Claims: The theoretical proofs are clear, smooth and rigorous.
Experimental Designs Or Analyses: My suggestions and concerns on the experimental part is in the Methods And Evaluation Criteria section. Thanks.
Supplementary Material: I think the supplementary material makes the theory proofs and experiment settings and explanations better.
Relation To Broader Scientific Literature: This is an interesting work which combines 2 popular methods in the modern ML systems and I believe it can have a broader impact in the future.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the valuable time and effort in providing detailed feedback on our work.
---
> **Q1:** The evidence is convincing in general, but I think it might be better to show their framework's robustness to privacy attacks since they mention that they combine the efficiency property of ICL and the privacy robustness of FL.
**A1:**
We thank the reviewer for the insightful question. We further conducted additional experiments to assess the privacy robustness of Fed-ICL. In particular, we evaluate the privacy robustness by Prompt Extraction Attacks [3], where each client generates responses to server queries using local knowledge, and we employ LLM to aim to reconstruct the original in-context examples using only the generated responses. Such a setup has been widely studied in previous works [1-4]. We list the prompt used for this reconstruction in Figure 4 ( https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure4.png ). We compared the reconstructed examples to the original ones, and the results of this comparison are presented in Figure 5 ( https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure5.png ).
Our findings indicate that even a strong model like GPT-4o struggles to accurately recover the original in-context examples, demonstrating the robustness of the Fed-ICL framework against Memory Extraction Attacks.
> **Q2:** Also, since these 2 datasets are in the area of QA, but right now more and more people care about the reasoning ability of LLMs, I wonder if this pipeline can still be effective in the reasoning tasks, which may make this work more impactful.
**A2:**
We thank the reviewer for the thoughtful feedback and for recognizing the contributions of our work. To the best of our knowledge, this study is the first to propose a framework that incorporates both in-context learning and federated learning with both theoretical and empirical support. We choose QA benchmarks such as MMLU and TruthfulQA following the previous works [6-11], which also study these two datasets in either federated learning or in-context learning.
Motivated by the reviewer’s comment and inspired by prior reasoning studies [12-14], we further evaluated the reasoning capabilities of Fed-ICL using a mathematical reasoning dataset. We focused on the GSM-MC benchmark [5], a multiple-choice variant of GSM8K, enabling the straightforward use of majority-vote aggregation at the server side. In this extended experiment, we ran the experiments in a federated learning setting by partitioning the training dataset among three clients without overlap. Each client was equipped with the GPT-4o-mini model with in-context length 5. We randomly sampled 100 questions from the test dataset to serve as the server query data, following previous work [15]. We then evaluated Fed-ICL’s performance by measuring the accuracy of the generated answers on these questions.
We show the results in Figure 1 ( https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure1.png ), which illustrates the performance progression of Fed-ICL and Fed-ICL-Free across communication rounds. The observed improvements over successive rounds indicate the robustness and effectiveness of Fed-ICL in addressing complex reasoning tasks.
[1] On the privacy risk of in-context learning. arXiv:2411.10512, 2024.
[2] Extracting training data from large language models. USENIX Security, 2021.
[3] Effective prompt extraction from language models. arXiv:2307.06865, 2023.
[4] Extracting prompts by inverting llm outputs. arXiv:2405.15012, 2024.
[5] Multiple-choice questions are efficient and robust llm evaluators. arXiv:2405.11966, 2024.
[6] Openfedllm: Training large language models on decentralized private data via federated learning. KDD, 2024.
[7] Fedbiot: Llm local fine-tuning in federated learning without full model. Proc. KDD, 2024.
[8] Understanding in-context learning from repetitions. arXiv:2310.00297, 2023.
[9] Symbol tuning improves in-context learning in language models. arXiv:2305.08298, 2023.
[10] Long-form factuality in large language models. arXiv:2403.18802, 2024.
[11] Large language models are human-level prompt engineers. ICLR, 2022.
[12] Gsm-symbolic: Understanding the limitations of mathematical reasoning in large language models. arXiv:2410.05229, 2024.
[13] Large language models as analogical reasoners. arXiv:2310.01714, 2023.
[14] A careful examination of large language model performance on grade school arithmetic. NeurIPS 37, 2024: 46819–46836.
[15] Improving factuality and reasoning in language models through multiagent debate. ICML, 2023.
[16] Few-shot In-context Learning on Knowledge Base Question Answering. ACL, 2023.
[17] Fedmatch: Federated learning over heterogeneous question answering data. CIKM, 2021. | Summary: This paper introduces Fed-ICL, a framework that enhances in-context learning (ICL) for QA tasks. Specifically, Fed-ICL leverages iterative interactions between clients and a central server, progressively refining responses while maintaining low communication costs (by transmitting the context). The authors provide theoretical convergence guarantees and demonstrate strong performance on standard QA benchmarks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: The method is novel compared to related works.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: **Strengths**
1. To the best of my knowledge, this work presents a novel idea by combining federated learning and in-context learning.
2. The paper is well-written.
3. The method is effective and supported by comprehensive experiments.
**Weaknesses**
1. The paper focuses only on the QA dataset, and it is unclear whether it can generalize to more challenging tasks.
2. Do the methods work for advanced models or even reasoning models? What if reasoning models do not require in-context exemplars?
Other Comments Or Suggestions: NA
Questions For Authors: What do the refined in-context exemplars look like, and how are they different from the original in-context exemplars?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the valuable time and effort in providing detailed feedback on our work.
---
> **Q1:** The paper focuses only on the QA dataset, and it is unclear whether it can generalize to more challenging tasks.
**A1:**
First, we would like to highlight that this work is the first to integrate in-context learning and federated learning, supported by both theoretical analysis and empirical validation. Our choice of QA benchmarks, including MMLU and TruthfulQA, aligns with prior work [2–7] in either federated or in-context learning. To explore more challenging tasks, and inspired by prior reasoning studies [8–10], we further evaluated Fed-ICL on GSM-MC [1], a multiple-choice variant of GSM8K for mathematical reasoning. We partitioned the training data across three non-overlapping clients, each using GPT-4o-mini with an in-context length of 5. Following prior work [11], we randomly sampled 100 test questions.
Results are shown in Figure 1 (https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure1.png), which illustrates the performance progression of Fed-ICL and Fed-ICL-Free over communication rounds. The consistent improvements highlight the robustness and effectiveness of Fed-ICL on more complex reasoning tasks.
> **Q2:** Do the methods work for advanced models or even reasoning models?
**A2:**
We believe our framework is broadly applicable to advanced and reasoning-oriented models, as it makes no assumptions about model architecture or output format. While we did not initially include experiments with such models, we conducted additional experiments inspired by the reviewer’s suggestion to assess Fed-ICL’s reasoning ability. As detailed in **A1**, our results on the GSM-MC benchmark demonstrate that Fed-ICL performs effectively on mathematical reasoning tasks, supporting the generality and robustness of our approach.
> **Q3:** What if reasoning models do not require in-context exemplars?
**A3:**
We argue that in-context exemplars often remain beneficial, even for advanced models [14–15]. To support this, we conducted additional experiments comparing four variants: Fed-ICL, Fed-ICL-Free, Fed-ICL-GT, and a baseline LLM without in-context exemplars, as suggested by the reviewer. We evaluated both a standard backbone (LLaMA-3.1-8B) and a more advanced one (GPT-4o-mini).
Consistent with our main paper, we used accuracy on MMLU and BERTScore on TruthfulQA. Results are shown in Table 1 (https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Table1.png) and Table 2 (https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Table2.png). Across both backbones and benchmarks, the baseline LLM without exemplars consistently underperforms the exemplar-based variants. This trend underscores the effectiveness of Fed-ICL and reaffirms the utility of in-context exemplars—even for more capable models.
> **Q4:** What do the refined in-context exemplars look like, and how are they different from the original in-context exemplars?
**A4:**
We show additional examples from TruthfulQA in Figures 2 ( https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure2.png ) and Figures 3 ( https://anonymous.4open.science/r/Fed-ICL_ICML_rebuttal-2D96/Figure3.png ) to illustrate how the data evolves throughout federated learning. We observe that the server outputs become more and more closer to the ground truth. The client's outputs become increasingly professional and detailed. These demonstrate the benefit of our interactive process.
## References
[1] Multiple-choice questions are efficient and robust LLM evaluators. arXiv:2405.11966, 2024.
[2] OpenFedLLM: Training large language models on decentralized private data via federated learning. KDD, 2024.
[3] FedBIoT: LLM local fine-tuning in federated learning without full model. KDD, 2024.
[4] Understanding in-context learning from repetitions. arXiv:2310.00297, 2023.
[5] Symbol tuning improves in-context learning in language models. arXiv:2305.08298, 2023.
[6] Long-form factuality in large language models. arXiv:2403.18802, 2024.
[7] Large language models are human-level prompt engineers. ICLR, 2022.
[8] GSM-Symbolic: Understanding the limitations of mathematical reasoning in large language models. arXiv:2410.05229, 2024.
[9] Large language models as analogical reasoners. arXiv:2310.01714, 2023.
[10] A careful examination of large language model performance on grade school arithmetic. NeurIPS, 2024.
[11] Improving factuality and reasoning in language models through multiagent debate. ICML, 2023.
[12] Few-shot in-context learning on knowledge base question answering. ACL, 2023.
[13] FedMatch: Federated learning over heterogeneous question answering data. CIKM, 2021.
[14] Meta-in-context learning in large language models. NeurIPS, 2023.
[15] Are emergent abilities in large language models just in-context learning? arXiv:2309.01809, 2023. | Summary: The paper proposes **Federated In-Context Learning (Fed-ICL)**, a framework for QA tasks that combines in-context learning and federated learning without transmitting model parameters. Fed-ICL enables clients to iteratively refine responses by sharing answers—not models—preserving privacy and reducing communication overhead. The authors provide theoretical guarantees of convergence and introduce **Fed-ICL-Free**, a variant for scenarios without labeled answers. Experiments on QA benchmarks show that Fed-ICL outperforms traditional FL and parameter-free methods, with ablation studies confirming the effectiveness of its components.
Claims And Evidence: Figure 2 and Figure 3 present the main experiments of the paper. They compare different methods, including FL-based approaches and various parameter-free methods. Through these experiments, the paper demonstrates the effectiveness of the proposed method. Additionally, the paper conducts ablation studies to showcase the robustness of the method. Section 4 provides the theoretical proofs.
Methods And Evaluation Criteria: To be honest, I’m not familiar with federated learning and haven’t done any research related to this area before. Therefore, I find it difficult to judge the novelty of the method proposed in the paper or evaluate its experimental setup. I’m unable to provide effective feedback on these aspects.
Theoretical Claims: Section 4.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Appendix A.
Relation To Broader Scientific Literature: Federated Learning, In context learning.
Essential References Not Discussed: None
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: None
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their valuable time and thoughtful feedback. We also appreciate your kind acknowledgment of our contributions to both the experimental and theoretical aspects of the work in Claims and Evidence. | Summary: The paper introduces Fed-ICL, a novel framework that blends federated learning with in-context learning to tackle question-answering tasks in a privacy-preserving manner. Fed-ICL operates in a round-based manner, iteratively refining answer quality through client-server communication. The authors support their framework with a theoretical convergence guarantee based on a simplified single-layer linear self-attention model and provide extensive experimental evaluations on benchmarks such as MMLU and TruthfulQA.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: No
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: Finding ans results
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strength: The paper makes a contribution by combining the ideas of federated learning and in-context learning. This integration is particularly valuable for applications with data privacy constraints and limited access to high-quality annotated examples. The inclusion of theoretical guarantees for convergence under a simplified linear model setting lends credibility to the proposed iterative refinement process and helps ground the empirical findings.
Weakness: The convergence guarantee is derived under a simplified linear self-attention model. While this is common for theoretical analysis, it remains an open question how these guarantees extend to more complex, fully nonlinear transformer architectures used in practice.
Other Comments Or Suggestions: None
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the valuable time and effort in providing detailed feedback on our work.
---
> **Q1:** The convergence guarantee is derived under a simplified linear self-attention model. While this is common for theoretical analysis, it remains an open question how these guarantees extend to more complex, fully nonlinear transformer architectures used in practice.
**A1:**
We appreciate the reviewer’s suggestion and agree that extending our theoretical analysis to more general transformer architectures is an important direction. In our current work, we establish convergence guarantees for a simplified linear self-attention model to provide theoretical insights that support our empirical findings. This modeling choice is in line with several recent works aiming to understand transformers under linear assumptions (e.g., [1], [2]). Extending the analysis to fully nonlinear transformer architectures is a challenging and independent research direction, which goes beyond the scope of our current work.
While analyzing fully nonlinear transformer architectures remains a significant challenge, we believe it is a promising and independent line of research. In particular, we conjecture that combining our framework with the recent results of [3], which show that an (L+1)-layer transformer can approximate L steps of in-context gradient descent (see their Section 3.5) could provide a pathway to deriving theoretical guarantees for federated in-context learning in more expressive models. However, we emphasize that such an extension is highly nontrivial and currently remains an open theoretical problem.
We will incorporate this expanded discussion into the final version of the paper, as suggested.
## References
[1] Transformers learn in-context by gradient descent. ICML, 2023.
[2] Trained transformers learn linear models in-context. JMLR, 2024.
[3] Transformers as statisticians: Provable in-context learning with in-context algorithm selection. NeurIPS, 2023. | null | null | null | null | null | null |
Unlocking the Power of SAM 2 for Few-Shot Segmentation | Accept (poster) | Summary: This paper utilizes SAM 2 and DINO-v2 to solve the few-shot segmentation problem. The authors first point out that the class-agnostic matching ability of SAM 2 is useful for few-shot segmentation, but SAM 2 focuses too much on the identity of objects, which makes it unsuitable for FSS. To address this issue, the authors propose Pseudo Prompt Generator to generate pseudo query memory and further optimize it using Iterative Memory Refinement and Support-Calibrated Memory Attention. The experimental results show that these methods achieve good performance on PASCAL-5i and COCO-20i datasets.
Claims And Evidence: Yes, the claims made in the submission are supported by clear and convincing evidence. The authors provide a comprehensive analysis of the limitations of SAM 2 in few-shot segmentation and demonstrate that the proposed methods can significantly improve the performance of few-shot segmentation tasks through extensive ablation studies and experiments on PASCAL-5i and COCO-20i datasets.
Methods And Evaluation Criteria: the proposed methods make sense for the few-shot segmentation problem. The authors introduce a novel approach that leverages the class-agnostic matching ability of SAM 2 to address the limitations of few-shot segmentation. The evaluation criteria are also well-defined, with experiments conducted on PASCAL-5i and COCO-20i datasets to validate the effectiveness of the proposed methods.
The only limitation is that the proposed methods are not tested on more challenging datasets to evaluate the generalization ability of the models, such as LVIS-92i or cross-domain datasets.
Theoretical Claims: Not applicable, as the paper does not contain any theoretical claims or proofs.
Experimental Designs Or Analyses: Yes, the authors follow traditional FSS settings and conduct extensive experiments to validate the effectiveness of the proposed methods. The ablation studies are also well-designed and comprehensive.
Supplementary Material: Yes, I review the additional implementation details and addtional experiments in the supplementary material.
Relation To Broader Scientific Literature: This paper is related to how to leverage foundation models to boost downstream vision tasks.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. The paper's logic is clear, with the authors first pointing out some limitations of SAM 2 in FSS and then proposing several reasonable modules to address these issues. The design of these modules may have an impact on future FSS research.
2. The experimental results are solid, with FSSAM showing significant improvements over the previous SOTA on PASCAL-5i and COCO-20i.
3. The ablation studies are comprehensive, demonstrating the effectiveness of each module and exploring the impact of some hyperparameters.
Weaknesses:
As I mentioned earlier, my main concern is the generalization ability of the model.
1. Previous works such as Matcher and GF-SAM achieved good results without additional fine-tuning on COCO, while FSSAM requires fine-tuning of some modules, which may affect the model's generalization ability. Is fine-tuning these modules necessary? If not fine-tuned, how much will the model's performance be affected?
2. The authors should test the model on more challenging datasets to validate the generalization ability of the model. For example, LVIS-92i, One-shot Part Segmentation, or some cross-domain datasets. (see Matcher, GF-SAM)
Other Comments Or Suggestions: In line 31, 'but some unexpected query background' seems like 'but' should be 'and'.
Questions For Authors: Instead of using DINO-v2, VRP-SAM using a trainable resnet also achieves competitive results. Can FSSAM use a trainable resnet instead of DINO-v2? Or, What will happen if FSSAM unfreezes the DINO-v2 backbone and fine-tunes it?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > Evaluation on LVIS-92$^i$.
Thanks for this precious suggestion, conducting evaluation on LVIS-92$^i$ that includes 920 classes can indeed show the **excellent generalizability** of our method. We select both Matcher and SINE (A Simple Image Segmentation Framework via In-Context Examples, NeurIPS'24) for comparisons. Since SINE is trained with COCO (80 classes) and directly test on LVIS-92$^i$, we directly take our trained FSSAM on COCO-20$^0$ (trained with 60 classes, under 1-shot setting) to perform evaluation on LVIS-92$^i$. Following Matcher and SINE, each fold comprises 2,300 testing episodes, and the 1-shot results are shown as follows:
|Method|Matcher|SINE|Ours|
|-|-|-|-|
|92$^0$|31.4|28.3|**34.7**|
|92$^1$|30.9|31.0|**37.8**|
|92$^2$|33.7|31.9|**37.2**|
|92$^3$|38.1|34.6|**41.1**|
|92$^4$|30.5|30.0|**33.9**|
|92$^5$|32.5|31.9|**38.1**|
|92$^6$|35.9|32.2|**40.6**|
|92$^7$|34.2|33.7|**38.9**|
|92$^8$|33.0|30.6|**36.9**|
|92$^9$|29.7|27.8|**33.8**|
|Mean|33.0|31.2|**37.3**|
|FB-IoU|66.2|63.5|**68.4**|
We can observe our FSSAM consistently outperform Matcher and SINE in all folds, showing **excellent generalizability** (COCO-20$^i$ $\to$ LVIS-92$^i$). We will include these comparisons in a newer version.
> Is fine-tuning SAM 2 necessary?
Yes, fine-tuning is necessary, and the reasons are as follows:
1. Original SAM 2's memory attention is trained for **same object matching**, while the matching of FSS is between *different query and support FG objects*, which we call it *incompatible FG-FG matching*. As we can observe from the table, with (w/) or without (w/o) fine-tuning (FT) show prominent performance gap.
2. FSSAM can consistently outperform SAM 2 by large margins, since we design modules to resolve the issue. However, FSSAM still requires fine-tuning, because the pseudo mask prompt is *inaccurate*, e.g., it covers *incomplete FG regions* and *unexpected BG regions*, which is different from SAM 2's mask prompt.
|Method|5$^0$|5$^1$|5$^2$|5$^3$|Mean|
|-|-|-|-|-|-|
|SAM 2 w/o FT|49.1|43.7|51.1|35.0|44.7|
|SAM 2 w/ FT|71.8|74.4|71.6|59.9|69.4|
|FSSAM w/o FT|61.9|59.8|61.0|51.4|58.5|
|FSSAM w/ FT|81.6|74.9|81.6|76.0|81.0|
Besides, in our response to your previous question, our FSSAM shows **excellent generalizability**, since our performance on LVIS-92$^i$ (the model is trained on COCO-20$^0$ and directly tested on LVIS-92$^i$) consistently outperform other methods by large margins.
> Typo in Line 31.
Thanks for your careful checking! We have corrected this typo.
> Can FSSAM use a trainable resnet instead of DINO-v2? What will happen if FSSAM unfreezes the DINO-v2 backbone and fine-tunes it?
Kindly remind DINOv2 is only responsible for generating pseudo mask prompt without learning, so it can be replaced as pretrained ResNet50, and there is no need to make it trainable. When we replace DINOv2 as ResNet50, the 1-shot mIoU on PASCAL-5$^i$ is 74.1, which is still much better than other methods (in Table 1). kindly note that FounFSS also uses DINOv2, and our performance is 4.2\% better.
For the second question, we can fine-tune DINOv2, but we need to design an extra learning objective to encourage better pseudo mask prompt, which may raise *inductive bias* issue (i.e., *degrading the generalizability*), since the setting of FSS is **training on some base classes while testing on unseen classes**. Besides, the *training cost would be much heavier*, since DINOv2-B has 86M parameters.
---
Rebuttal Comment 1.1:
Comment: Thanks for the detailed response and the additional experiments on LVIS-92, which effectively address my concerns regarding generalization. I also appreciate the clarification on the necessity of fine-tuning and the role of DINOv2. I will increase my score to 4.
In addition, after reviewing Reviewer HtbM’s comments, I would like to share that I am also very familiar with related works such as SegGPT, Matcher, and SINE. I agree with the authors that the comparison with SINE may not be entirely fair, as SINE benefits from in-domain training data. The strong performance of FSSAM on LVIS-92i provides compelling evidence of its superior generalization ability. That said, including results on one-shot part segmentation would further strengthen the paper.
---
Reply to Comment 1.1.1:
Comment: Sincerely thanks for your recognition of our work, as well as your explanation to Reviewer HtbM's comment! Following your suggestions, we further conduct evaluation on on-shot part segmentation dataset PASCAL-Part. Specifically, we still use the model trained on COCO-20$^0$ to directly perform evaluation, and the 1-shot results are as follows.
|Method|F-0|F-1|F-2|F-3|mIoU|
|-|-|-|-|-|-|
|Matcher|**37.1**|56.3|32.4|45.7|42.9|
|Ours|29.5|**73.1**|**34.9**|**48.0**|**46.4**|
We can observe that our method still outperforms better than baseline Matcher in all folds except fold 0. To figure out the reasons, we visualize the test samples of fold 0, and find that DINOv2 cannot generate very good pseudo mask prompts for these classes, leading to relative low scores. Particularly, in fold 1, our method can surpass Matcher by 16.8\%, and we attribute it to the fact that DINOv2 can generate quite good mask prompts for the classes in this fold. We will include such evaluation in our paper. | Summary: This paper leverages SAM2’s strong matching ability to do the few-shot segmentation. Considering the matching of SMA2 is for sam2-object matching, the paper introduces Pseudo Prompt Generator (PPG) to generate pseudo query memories, and further design Iterative Memory Refinement (IMR) to supplement this memory with more query FG features, and devise a SupportCalibrated Memory Attention (SCMA) to mitigate the side-effects of unexpected BG features in pseudo memory.
Claims And Evidence: The claims are clear and convincing.
Methods And Evaluation Criteria: The paper presents results on COCO and PASCAL, which are standard FSS datasets. However, it would be valuable to also evaluate on LVIS-92$^i$[1], which is a more challenging benchmark for evaluating the generalization of a model across datasets based on LVIS.
[1] Liu, Yang, et al. "Matcher: Segment anything with one shot using all-purpose feature matching." arXiv preprint arXiv:2305.13310 (2023).
Theoretical Claims: The equations look good to me.
Experimental Designs Or Analyses: The experimental designs and analyses (for the ablation study) look good to me. Please see the weakness for other issues
Supplementary Material: I reviewed the additional experiments, additional results and additional figures (especially the additional visualization)/
Relation To Broader Scientific Literature: The paper explores the potential of SAM2 for few-shot segmentation, leveraging its strong matching capability and extending it beyond object-specific matching to include class-level matching across different identities.
Essential References Not Discussed: The paper didn’t discuss a very related paper: [NeurIPS'24] A Simple Image Segmentation Framework via In-Context Examples. And the evaluation result couldn’t beat the results in SINE [2]. (see Table 1 in SINE)
[2] Liu, Yang, et al. "A Simple Image Segmentation Framework via In-Context Examples." The Thirty-eighth Annual Conference on Neural Information Processing Systems.
Other Strengths And Weaknesses: **Strengths**
- Effectively leverages SAM 2’s memory bank matching for few-shot segmentation.
- Comprehensive ablation studies validate each proposed module.
**Weaknesses**
- The pipeline is relatively complex, and the performance seems to fall behind SINE, which is simpler and can perform more tasks. (this is my major concern).
- The paper lacks a discussion of failure cases and potential limitations.
- The visualization results are insufficient. While most of them are effective—such as the comparisons between FG Prior and Disc Prior, as well as the memory refinement across different iterations—the model's results are not compared with segmentation results from other prior models (as well as the original sam2 model's result). Please include these additional visualizations.
Other Comments Or Suggestions: NA
Questions For Authors: - As the paper points out, the number of memory iterations should be traded off for better performance. Is there a way to find the optimized iteration for each case adaptively?
- This work primarily focuses on refining the mask memory. Given the strong prompting capability of SAM2, would it be possible to generate prompt points on the target object region and use these prompts in the mask decoder to obtain the final output?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Evaluation on LVIS-92$^i$.
Conducting evaluation on LVIS-92$^i$ (920 classes) can show the **excellent generalizability** of FSSAM. We select both Matcher and SINE for comparisons. Since SINE is trained with COCO (80 classes) and directly test on LVIS-92$^i$, we directly take our trained 1-shot FSSAM on COCO-20$^0$ (60 classes) for fair evaluation. Following baselines, each fold comprises 2,300 testing episodes, and the 1-shot results are as follows:
|Method|Matcher|SINE|Ours|
|-|-|-|-|
|92$^0$|31.4|28.3|**34.7**|
|92$^1$|30.9|31.0|**37.8**|
|92$^2$|33.7|31.9|**37.2**|
|92$^3$|38.1|34.6|**41.1**|
|92$^4$|30.5|30.0|**33.9**|
|92$^5$|32.5|31.9|**38.1**|
|92$^6$|35.9|32.2|**40.6**|
|92$^7$|34.2|33.7|**38.9**|
|92$^8$|33.0|30.6|**36.9**|
|92$^9$|29.7|27.8|**33.8**|
|Mean|33.0|31.2|**37.3**|
|FB-IoU|66.2|63.5|**68.4**|
We can observe our FSSAM consistently outperform Matcher and SINE in all folds, showing **excellent generalizability** (COCO-20$^i$ $\to$ LVIS-92$^i$). We will include these results in a newer version.
> (Major concern) Compare with SINE [2] on PASCAL-5$^i$ and COCO-20$^i$.
SINE CANNOT be fairly compared on these datasets:
1. FSS models are trained on some **base classes**, then tested on **unseen classes**, i.e., the testing samples are **out-domain** ones.
2. In Section 4.2 of SINE, authors mention "SINE is trained with all data of COCO". Specifically, COCO and PASCAL have 80 and 20 classes, and COCO's classes include PASCAL's classes. Since SINE is trained on whole COCO, **it has learned to deal with all classes of PASCAL and COCO during training**, i.e., the testing samples are **in-domain** ones. Since SINE has been trained with the test classes (in each fold of FSS), its scores will naturally be higher than FSS methods. Unless we remove COCO from SINE's training set, SINE **can never be fairly compared on PASCAL-5$^i$ and COCO-20$^i$**.
3. That being said, fair comparisons can be conducted on LVIS-92$^i$, and the results are included in previous question, where our method surpasses SINE by **6.1\% mIoU**, under the consistent **out-domain** setting of "training on COCO and directly testing on LVIS-92$^i$".
> Failure cases and limitations.
There is one failure case/limitation. Kindly remind our method relies on **pseudo mask prompt** to resolve the *incompatible FG-FG matching issue*. In some very difficult examples (all baselines cannot deal with such cases), e.g., the FG and BG are very similar and are quite difficult to distinguish, the generated pseudo mask prompt may be *misleading*, e.g., *the real FG is completely uncovered*. This motivates us to further design an error correction module, and we leave it as a future direction. We will include some failure cases in a newer version.
> Insufficient visualization.
Thanks for this suggestion! We will include some baselines' results for comparisons in a newer version.
> Can iteration number (in IMR) be adaptive?
The iteration number can theoretically be adaptive, yet there exist some challenges, and we uniformly fix it as 3 (see Table 4). Let's recall (1) the impact of IMR, and (2) when to use more iterations.
For (1), IMR will **make the incomplete FG regions in pseudo mask prompt complete**, but at risk of *introducing unexpected BGs (noises)*. Generally, using more iterations can make FG regions more complete, but introduce more noises, so trade-offs should be made to determine the iteration number.
For (2), we dive into the test samples, and find that **difficult samples, containing either multiple FG objects or complex BG, require larger iteration number**. The initial pseudo mask prompt of these difficult samples can **only cover limited FG regions**, so more iterations are required to make FG regions complete (to be a better prompt).
Hence, whether the iteration number can be adaptive depends on if such difficult samples can be automatically identified or not. Unfortunately, determining the difficulty of each case is not trivial, i.e., we cannot either *measure the number of FG objects in query images* or *judge whether query FG and BG are easy to distinguish or not*, and we leave it as a future direction.
> Can we use point prompt?
Yes, but it's not a good choice compared to pseudo mask prompt, since:
1. Although we can find some points (in query) with largest similarities to support FG features as point prompts, the overall framework is not easy to optimize, i.e., it's hard to determine if a point is the best candidate or not.
2. 1 point prompt can only correspond to 1 entity. When there are multiple FG objects in a query image, e.g., 20 people, it's very difficult to automatically find 1 point for each people. If any people is not assigned with point prompt, he will be classified as BG.
3. Instead, pseudo mask prompt can be regarded as a special case of point prompt, which can (1) make optimization easier, and (2) include sufficient points (to cover each FG object).
---
Rebuttal Comment 1.1:
Comment: Thank you to the authors for the detailed response. The explanation of SINE, along with Reviewer ZVAB’s comment, and the results on LVIS-92$^i$ have addressed my major concerns. I also appreciate the thorough responses to the other questions. I will increase my score to 3.
---
Reply to Comment 1.1.1:
Comment: Sincerely thanks for taking your time to review our paper and provide the valuable suggestions! We will follow your suggestions to include more visualizations, failure cases, and more evaluations on LVIS-92$^i$ in a newer version. | Summary: This paper presents FSSAM, which leverages SAM2 for few-shot segmentation.
FSSAM designs a Pseudo Prompt Generator to generate pseudo query memories, an Iterative Memory Refinement to iteratively refine pseudo query memories, and a Support-Calibrated Memory Attention to suppress background noise.
Extensive experiments demonstrate state-of-the-art performance.
Claims And Evidence: N/A
Methods And Evaluation Criteria: N/A
Theoretical Claims: N/A
Experimental Designs Or Analyses: N/A
Supplementary Material: N/A
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths
- The idea of employing SAM2's Foreground-Foreground matching ability in video segmentation to measure feature similarities between query and support in few-shot segmentation is interesting.
- FSSAM designs several effective modules to make SAM2 adapt to few-shot segmentation. Extensive quantitive and qualitative analysis enhances its interpretability.
- The proposed method outperforms the existing SOTA on two benchmarks.
Weaknesses
- FSSAM uses SAM2 and DINOv2, which may have a larger number of parameters than other methods and result in additional computational cost.
- It's an interesting work but lacks substantive discussion. What was the most important finding in this work? Is the main finding that SAM2 can be used for FSS, or can a memory-based video segmentation model be used for FSS through the proposed module?
- The previous approaches usually obtain better results using a larger model. Table 7 in the appendix explores the impact of different backbones on performance. It can be found that using a larger backbone does not bring consistent improvement. Does it indicate that the method has poor scalability?
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Larger number of parameters than other methods and result in additional computational cost.
Thanks for this comment. Our parameter number is actually much smaller than most of foundation-based FSS methods. We select some methods and summarize their parameter number, learnable parameter number, as well as the 1-shot mIoU scores on PASCAL-5$^i$ as follows:
|Method|#Params (M)|#Learnable Params (M)|mIoU|
|-|-|-|-|
|HDMNet|51|4|69.4|
|AMNet|54|7|70.1|
|HMNet|62|15|70.4|
|Matcher|941|0|68.1|
|VRP-SAM|666|2|71.9|
|GF-SAM|941|0|72.1|
|FounFSS|87|1|76.8|
|Ours|132|11|81.0|
The first 3 rows correspond to classical FSS methods that use ResNet50 as the pretrained backbone, and the remaining methods refer to foundation-based FSS methods that use DINOv2 and/or SAM. For our finalized model, we use DINOv2-B (86M) and SAM 2-S (46M) without extra parameters (kindly remind our proposed modules are parameter-free), and fine-tune part of SAM 2's parameters.
It can be observed from the table:
1. Among foundation-based FSS methods, our parameter number is much smaller than most of them, while our performance is consistently much better.
2. Compared to classical FSS methods, though we use more parameters, the difference is not as large as expected, while the performance gap is quite prominent, so we believe the additional cost is worthy.
For **computational complexity**, the designed modules will introduce additional **linear complexity** to the original foundation model, which have already been described in "Memory Complexity" of Section 4.2 and 4.3.
Therefore, the computational burden of our FSSAM is reasonable and acceptable.
> Substantive discussion about the most important finding. Is the main finding that SAM 2 can be used for FSS, or can a memory-based video segmentation model be used for FSS through the proposed module?
Our main finding is **memory-based video segmentation model can be used for FSS through the proposed modules**, and we focus on one of the most representative and powerful models, i.e., SAM 2.
In Table 1, baselines Matcher, VRP-SAM and FG-SAM uniformly deploy SAM-L for FSS, where SAM-L (641M) is much larger than the one we deployed, i.e., SAM 2-S (46M).
As shown in the first row of component-wise ablation study in Table 3, naive SAM 2-S cannot outperform any of these baselines, and we attribute it to the facts that (1) our SAM 2-S (46M) is much smaller than their SAM-L (641M), and (2) there exist an *incompatible matching issue* (as introduced in Section 1).
After using our designed modules to resolve this issue, our FSSAM can use much fewer parameters to outperform these foundation-based FSS methods by large margins, showing the effectiveness of our design, serving as our main finding.
> Larger backbone cannot guarantee consistent improvement.
We would like to make the following notes to Table 7:
1. We study 3 versions of SAM 2, including S (46M), B (80.8M) and L (224.4M). According to the official Github of SAM 2, *SAM 2-B (80.8M) originally CANNOT outperform SAM 2-S (46M) in 2 out of 3 datasets*, so it's reasonable that adapting SAM 2-B (80.8M) for FSS cannot show comparable performance as SAM 2-S (46M). When we remove SAM 2-B (80.8M), the improvement is stable, e.g., the mIoU is increased from 81.0 (SAM 2-S, DINOv2-B) to 81.5 (SAM 2-L, DINOv2-B).
2. DINOv2 is only responsible for generating cosine similarity-based pseudo mask prompt, **whose features will not be directly used in other modules**, thus upgrading DINOv2 from from B (86M) to L (300M) cannot guarantee better performance, i.e., the pseudo mask prompt generated by DINOv2-B is good enough.
In summary, using larger backbone (SAM 2) can guarantee improvement.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for responding to my concerns. According to the rebuttal, the authors claim that the main finding is "memory-based video segmentation model can be used for FSS through the proposed modules".
I think it should be comprehensively evaluated using different memory-based video segmentation models.
So I keep my rating.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank you for providing precious suggestions, including the initial ones and the latest one of trying different memory-based video segmentation models. We agree with you it would make our proposed modules stronger, as they can be used like "plug-ins" in this way, for memory-based video segmentation models. Unfortunately, we cannot finish training these new models in this short discussion period. That being said, we will incorporate your other comments into our paper first, and include the "plug-in" experiments once complete. | Summary: The paper introduces the Few-Shot Segment Anything Model (FSSAM), a novel method that leverages the powerful matching capabilities of SAM 2 to enhance few-shot segmentation tasks. The authors address the challenge of adapting SAM 2's same-object matching ability to the different-object matching required in few-shot segmentation by proposing the Pseudo Prompt Generator (PPG), which generates pseudo query memories using prior masks to enable compatible matching between support and query features. To further refine these memories and suppress background noise, the paper introduces the Iterative Memory Refinement (IMR) module, which iteratively incorporates more complete foreground features, and the Support-Calibrated Memory Attention (SCMA) module, which suppresses unexpected background features during the attention process. Extensive experiments on PASCAL-5i and COCO-20i benchmarks demonstrate state-of-the-art performance, with significant improvements in the averaged mIoU and FB-IoU compared to previous methods.
Claims And Evidence: The claims made in the submission are generally well-supported by clear and convincing evidence. The authors provide a comprehensive approach to adapting SAM 2 for few-shot segmentation tasks and demonstrate its effectiveness through both quantitative and qualitative results.
Methods And Evaluation Criteria: The proposed methods (PPG, IMR, SCMA) and evaluation criteria (mIoU, FB-IoU on PASCAL-5i and COCO-20i) are relevant and appropriate for the problem of few-shot segmentation. They address key challenges in adapting SAM 2 to this task and provide a comprehensive evaluation of the model's performance. The methods are well-supported by both quantitative results and qualitative visualizations, making them suitable for the application at hand.
However, it would be beneficial to include a comparison with versions of these methods that incorporate learnable parameters. This would help demonstrate the impact of learnable parameters on the model's adaptability and performance, and further validate the robustness of the proposed approach in different scenarios.
Theoretical Claims: Two A_QQ appear in Figure 3, and in conjunction with Equation (8), do these instances carry different meanings? Additionally, the correlation between Figure 2, "Overview of FSSAM," and the detailed descriptions of each module in the Methodology section appears somewhat inconsistent. More specifically, the relationship between the illustration of IMR in Figure 3 and the overview presented in Figure 2 seems somewhat confusing.
Experimental Designs Or Analyses: The selection of datasets, evaluation metrics, and ablation studies offers a comprehensive assessment of the proposed method's performance.
However, in the "Parameter Study on IMR" analysis, the performance decreases when the iteration n is equal to 4, yet it increases in 5^3. Is there any further analysis?
Supplementary Material: The supplementary material provides support for the paper. It includes detailed implementation details, additional experiments, and visualizations that validate the effectiveness, robustness, and stability of the proposed method (FSSAM). The analysis of different model sizes and the impact of SCMA further strengthens the design choices and contributions claimed in the main paper.
Relation To Broader Scientific Literature: The paper leverages recent advancements in foundation models, pseudo prompt generation, iterative refinement, and attention mechanisms to address the challenges of adapting SAM 2 for few-shot segmentation. The comprehensive evaluation and ablation studies further validate the effectiveness of the proposed methods.
Essential References Not Discussed: No
Other Strengths And Weaknesses: The paper leverages the strengths of SAM 2 to address the challenges of few-shot segmentation. The key contributions include the Pseudo Prompt Generator (PPG) for creating compatible pseudo query memories, the Iterative Memory Refinement (IMR) module for enhancing foreground features, and the Support-Calibrated Memory Attention (SCMA) to suppress background noise during segmentation.
While the experiments are comprehensive and demonstrate performance improvements, there is room for deeper analysis. Specifically, further investigation into the impact of computational trade-offs, and the influence of learnable parameters could provide additional insights and strengthen the overall robustness of the proposed method.
Other Comments Or Suggestions: There appears to be a discrepancy between the data in Table 4, where the value for n=3 in 5^3 is 76.0, and the corresponding value in Table 1 is 75.9.
Using the same symbol AQQ for different quantities can indeed lead to confusion. To improve clarity, it would be advisable to use distinct symbols in Equation (13).
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > Computational burden and learnable parameters.
Thanks for your valuable suggestion! We agree it would be better to include the **parameter number** for further comparisons. We select some methods and summarize their parameter number, learnable parameter number, as well as the 1-shot mIoU scores on PASCAL-5$^i$ as follows:
|Method|#Params (M)|#Learnable Params (M)|mIoU|
|-|-|-|-|
|HDMNet|51|4|69.4|
|AMNet|54|7|70.1|
|HMNet|62|15|70.4|
|Matcher|941|0|68.1|
|VRP-SAM|666|2|71.9|
|GF-SAM|941|0|72.1|
|FounFSS|87|1|76.8|
|Ours|132|11|81.0|
The first 3 rows correspond to classical FSS methods that use ResNet50 as the pretrained backbone, and the remaining methods refer to foundation-based FSS methods that use DINOv2 and/or SAM. For our finalized model, we use DINOv2-B (86M) and SAM 2-S (46M) without extra parameters (kindly remind our proposed modules are parameter-free), and fine-tune part of SAM 2's parameters. It can be observed: (1) Among foundation-based FSS methods, our parameter number is much smaller than most of them, while our performance is consistently much better; (2) Compared to classical FSS methods, though we use more parameters, the difference is not as large as expected, while the performance gap is quite prominent, so we believe the additional cost is worthy.
For **computational complexity**, the designed modules will introduce additional **linear complexity** to the original foundation model, which have already been described in "Memory Complexity" of Section 4.2 and 4.3.
Therefore, the computational burden of our FSSAM is reasonable and acceptable.
> Comparison with versions of these methods that incorporate learnable parameters.
This comment locates in "Methods And Evaluation Criteria", sorry but we are confused about "**different versions**", do you mean **using SAM 2 and DINOv2 with different sizes** or something else?
If our understanding is correct:
1. FSSAM is built upon SAM 2 and DINOv2 **without additional parameters**, the designed modules are **parameter-free**, so the variants in Table 3 have same (learnable) parameters.
2. All parameters of DINOv2 are frozen. For SAM 2, we **fine-tune its memory encoder, memory attention and mask decoder**.
3. Different SAM 2 mainly differ in image encoders, and **the learnable parameters of FSSAM are uniformly 11M**, regardless of which size is used.
4. We have studied the impacts of different sizes in Table 7. For your convenience, we summarize some statistics as follows.
|SAM 2|DINOv2|#Params (M)|#Learnable Params (M)|mIoU|
|-|-|-|-|-|
|S|B|132|11|81.0|
|S|L|346|11|80.6|
|B|B|167|11|79.9|
|B|L|381|11|79.8|
|L|B|310|11|81.5|
|L|L|524|11|81.1|
After making trade-offs between computational burden and performance, we use SAM 2-S (46M) and DINOv2-B (86M). For reasons why using larger SAM 2 and DINOv2 cannot guarantee performance gain, please refer to our reponses to **Larger backbone cannot guarantee consistent improvement** of **Reviewer pnf2**.
> Same symbol $A_{QQ}$ in different modules.
Thanks for this comment. They uniformly refer to the mutual similarities between two features, but we do agree it would be much better to differentiate them in different modules, e.g., additionally include module names as superscripts.
> Inconsistency between Figure 2 and detailed description in Section 4.
Thanks for pointing out this issue, we will modify them accordingly.
> Confusing relationship between IMR in Figure 2 and Figure 3.
We guess that the confusion comes from the inconsistent outputs of IMR modules in Figure 2 and 3, we will unify them in a newer version.
> In "Parameter study on IMR", performance decreases when the iteration n is 4, yet it increases in fold 5$^3$.
The test classes of fold 5$^3$ comprise of potted plant, sheep, sofa, train, and tv/monitor, and we find that the samples of this fold are more challenging than those in other 3 folds (e.g., the performance of fold 5$^3$ is consistently the worst among all folds for all methods in Table 1). Specifically, many samples from this fold include: (1) multiple tiny objects, and (2) complex background (BG), making it hard to distinguish FG and BG. Therefore, the initially generated prior masks in fold 5$^3$ CANNOT cover sufficient FG regions, and **requires larger n** in IMR to **complete FG regions**.
Kindly remind with the increase of n, more unexpected BG regions will also be activated, acting as some noises to prevent from boosting the performance. Therefore, n should not be too large, otherwise, the performance (e.g., that of fold 5$^0$, 5$^1$ and 5$^2$) will decrease.
In Table 4, we conduct experiments to verify the impacts different iteration number, and we uniformly set it as 3 for all folds currently. We think a better way is **adaptively determining the iteration number n for each sample**, and we will leave it as a future direction.
> Discrepancy between the data in Table 1 and 4.
Thanks for your careful checking! We will correct the value in Table 1.
---
Rebuttal Comment 1.1:
Comment: The authors have addressed most of my concerns. I will raise my score to 3.
---
Reply to Comment 1.1.1:
Comment: We appreciate your time spent on reviewing our paper, as well as the valuable suggestions! We are pleased to hear most of your concerns have been addressed, and we will follow your suggestions to include the parameter information and address other issues like typos. | null | null | null | null | null | null |
Jacobian Sparse Autoencoders: Sparsify Computations, Not Just Activations | Accept (poster) | Summary: **Summary**
Sparse Autoencoders (SAEs) help interpret latent activations in LLMs but do not explicitly reveal how computations are performed. This paper extends SAEs to study the sparsity of the computational transformations within MLP layers of transformer-based LMs. The authors train two SAEs—one before and one after an MLP transformation—and enforce sparsity in the Jacobian of the input-output mapping. This is done via an $\ell_1$ penalty on the Jacobian, encouraging learned features to be sparse linear functions of each other. To make this tractable, the paper introduces optimizations leveraging the inherent sparsity of SAE latents. Main results: (a) JSAEs induce Jacobian sparsity without significantly degrading reconstruction quality, (b) Trained LMs exhibit greater computational sparsity than randomly initialized ones, indicating that sparsity is a learned property, (c) Jacobian sparsity is a reasonable proxy for computational sparsity since the JSAE+MLP mapping is approximately linear.
**Strengths**
- JSAEs extend recent SAE-based interpretability techniques from analyzing activations to analyzing computations, providing a more structured view of how LLMs process information. The problem is formulated in a clean and well-motivated way. The paper also does a great job at differentiating JSAEs from standard SAEs and transcoders, clearly explaining the conceptual differences in what each method sparsifies.
- The proposed optimizations make Jacobian regularization computationally feasible for large models, where naive Jacobian computation would be intractable. JSAEs only increase compute by ~2x compared to standard SAEs.
- Evaluation metrics demonstrate minimal trade-offs between sparsity and reconstruction fidelity, suggesting that the Jacobian penalty does not significantly degrade representation quality.
- Strong empirical results show that JSAEs extract meaningful structure rather than fitting noise, as demonstrated in the random initialization ablation. Trained LMs exhibit far greater Jacobian sparsity than randomly initialized ones, suggesting that JSAEs capture properties learned during training.
**Weaknesses**
- The paper provides a tool to study MLP computaion but does not use it to provide new insights into MLP computation. For example, the work would be stronger with case studies showing what JSAEs reveal about computation: Can JSAEs recover known mechanistic circuits in toy models? Do they expose meaningful functional structures in large LMs? How would an interpretability researcher use JSAEs to answer practical questions about LLM internals?
- The study focuses on reconstruction and sparsity metrics, but does not evaluate whether JSAE features are useful for real-world interpretability tasks. The study should use recent benchmarks for SAEs to incorporate additional metrics. AxBench (https://arxiv.org/abs/2501.17148) evaluate SAE features for concept detection and model steering and SAEBench (https://www.neuronpedia.org/sae-bench/info) provides structured metrics for assessing interpretability and feature usefulness. Comparing JSAEs to these benchmarks would make the empirical results more convincing.
- The method is specialized for MLP modules and does not consider attention mechanisms, residual streams, or full transformer computations. It focuses on single MLP layers, making it unclear how JSAEs scale to studying entire transformer models with hundreds of MLPs. This limitation suggests that JSAEs may be more suited for local rather than global interpretability.
- Missing related work on interpretability techniques that focus on model computation. Shah et al. (https://arxiv.org/abs/2404.11534) uses linear surrogate models to analyze how model components (e.g., conv filters in vision models, MLPs) in a trained neural network contribute to final model outputs. Similarly, Balasubramanian et al. (https://arxiv.org/abs/2406.01583) uses attribution techniques to quantify the role of individual components in shaping vision model representations.
Claims And Evidence: Yes. Please see my review above
Methods And Evaluation Criteria: Please see my review above
Theoretical Claims: Yes, the appendix on efficiently computing MLP Jacobians.
Experimental Designs Or Analyses: Please see my review above
Supplementary Material: Skimmed it
Relation To Broader Scientific Literature: Please see my review above
Essential References Not Discussed: Please see my review above
Other Strengths And Weaknesses: Please see my review above
Other Comments Or Suggestions: Please see my review above
Questions For Authors: Please see my review above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your positive comments and useful recommendations.
### Qualitative results and insights
We have updated the manuscript with qualitative [results](https://anonymous.4open.science/r/jacobian-saes-icml-D7BF/jacobian-saes-icml-examples.pdf). Specifically, we plot max-activating examples for an output feature, and the 16 input features that connect to it most strongly. The very first output latent (34455) in that document that activates fairly generally on German text. The input latents respond to:
* Tokens that frequently appear in German text. There is an input that mainly responds to "Pf", and another that responds to "sch", and another that responds to "Kle".
* "German"
* "von"
* Place names such as "Austria" and "Berlin"
There are also far more subtle examples, such as output latent 52843 (easiest to Ctrl-F). This latent is activated by "go" and "goes" in different figurative contexts, including "go on record" and "go behind his back"; it does not appear to respond to the literal meaning of movement through space. This distinction may be part of what this circuit is designed to clarify. One of the corresponding inputs include measure of extent and distance, like "a long way" and "right to the 6 th floor" and another to the word "back" in "go back". Other input latents include "go" in a figurative context, or words that have a similar role to "go" such as "proceed", "headed" and "come" and even one responding to "GO" or "GOTO" in computer code.
Note that the output features are not hand-picked, but are ordered starting with the output with the largest element of the Jacobian averaged across all inputs.
### Evaluation
These benchmarks were not available on the ICML submission date ([1] was published in March, and [2] was published in very late January).
As such, we plan to run them for the camera ready.
[1] https://arxiv.org/abs/2503.09532
[2] https://arxiv.org/abs/2501.17148
### Other model components
We agree that we used JSAEs only on MLPs, i.e. in the local interpretability setting, as it was a useful starting point to introduce the JSAE methodology.
We note that other interpretability methods, e.g. SAEs and transcoders, were also initially developed only on a single MLP at a time.
To understand out approach to moving towards using JSAEs to obtain a global understanding of LLMs, it is worth stepping back and thinking an overall approach in the interpretability literature, of which the JSAE forms a part. Perhaps the most exciting recent work following this approach is the Anthropic circuit tracing paper, which was published only a few days ago, and cites our work.
The key idea in our work and [3] is:
* Take multiple layers in network.
* Decompose each layer into sparse latents (we use SAEs at different layers, Anthropic use transcoders at different layers).
* Take the Jacobian for the mapping from sparse latents at one layer to sparse latents at later layers.
* Identify strong connections using large elements in that Jacobian.
* Interpret those connections (which is much _much_ easier if the connections are sparse).
In any such approach, whether local (our current work) or global ([3]), the Jacobians are denser than they could be, simply because we don't have a term in the loss that explicitly encourages them to be sparse.
Our key insight was that it is actually possible to develop an efficient loss term that sparsifies Jacobians.
While we initially only applied this loss term to MLPs, the overall approach certainly could be applied globally, indeed, we are super-excited about further sparsifying the Jacobians between transcoders latents studied in [3] to get even sparser, more interpretable global circuits.
[3] https://transformer-circuits.pub/2025/attribution-graphs/methods.html
### Additional Related work
Thanks! We have added this to the Related Work section in our working manuscript.
### Conclusion
Thank you for generously outlining the paper's strengths in your original review.
We hope this response (and especially the new qualitative results) have addressed your key concerns.
If so, we would greatly appreciate it if you would reconsider your score.
---
Rebuttal Comment 1.1:
Comment: Thanks for addressing some of my concerns. I have increased my score.
---
Reply to Comment 1.1.1:
Comment: Thanks so much for carefully considering our rebuttal and increasing your score!
We hope that our new qualitative results have addressed the main concern of all the reviewers. However, ZBhh has just ticked the box without commenting on the rebuttal, and has not changed their score from a 1. Therefore, the paper will likely need an extra bump to get accepted.
If you think the paper should be accepted, we were wondering whether you'd give us that bump by again considering your score? | Summary: The authors introduce Jacobian SAEs, as a form of dictionary learning that also facilitates circuit analysis by creating sparse computational graphs. They jointly train SAEs on both input and output to an MLP layer, and make the Jacobian sparse by adding its L1 norm to the loss function.
Though computing and differentiating the Jacobian is extremely complicated naïvely, the process is made tractable by analytically computing the Jacobian, leveraging the simple mathematical form of an MLP. Only standard MLPs studied, not the gated MLPs used in most common most modern models. Since only the k active latents matter, the operation only doubles the cost in the context, though the exact computational complexity as models scale isn't explored.
The most relevant prior work is transcoders which replace MLP layers with a wider sparser replacement. The authors argue that Jacobian SAEs are distinct as transcoders sparsify computation while their method sparsifies input and output.
To show JSAE effectiveness, they demonstrate:
- While Jacobian sparsity regularization degrades other metrics there's a sweet spot with reasonable performance and better sparsity
- Cross-entropy and explained variance are comparable to normal SAEs
- Auto-interpretability scores are comparable to normal SAEs
- They find sparser Jacobians with trained JSAEs on trained transformers than randomly initialised ones
To validate the approach of studying gradients to understand the computation of the MLP layer, on a given prompt they vary each SAE input latent to see effects on each output latents. They show that 88% of relationships are linear, many are ReLU like, and some are more complex
Claims And Evidence: See below
Methods And Evaluation Criteria: See below
Theoretical Claims: N/A
Experimental Designs Or Analyses: See below
Supplementary Material: No
Relation To Broader Scientific Literature: See below esp re transcoders
Essential References Not Discussed: No
Other Strengths And Weaknesses: See below
Other Comments Or Suggestions: ## Major Comments
*The following are things that, if adequately addressed, would increase my score*
Summary; I overall consider this paper to be a weak accept. I think it provides some innovative new ideas, in particular using Jacobians as a way to measure the sparsity of a computational graph and tricks for how to compute and train this well. However, I don't feel that the authors provide a compelling enough argument for why one would prefer these over prior techniques like transcoders. If I were convinced there were compelling use cases where one would prefer JSAEs, I would be a lot more excited about this paper.
1. The paper doesn't clearly explain why I should prefer this method over transcoders. Transcoders already provide sparsity in their output, as the output is essentially a sparse linear combination of the decoder vectors from transcoder units. The main difference seems to be that transcoders don't explicitly sparsify the input, only the output. However, it’s unclear why sparsifying the input is especially valuable or significant. The input vector of a transcoder latent can be projected onto a normal residual SAE's decoder to see which concepts are used, though perhaps that would have too much interference?
One potential advantage of JSAEs could be clearer representation in cases where multiple transcoder latents share identical decoders. JSAEs would represent this scenario more cleanly with a single output latent.
If any of these differences matter, the paper should explicitly explain why and ideally provide a concrete example.
2. More broadly, the paper doesn't clearly motivate why Jacobian SAEs are interesting or practically useful. I'm sympathetic to the idea that high-quality circuit analysis with interpretable nodes is valuable, and am excited about improved techniques there. However, if you're trying to argue that JSAEs improve interpretability compared to methods like sparse feature circuits on normal SAEs or transcoders, then clear empirical evidence is needed. For example, analyzing tasks or contexts studied in [Dunefsky et al.](https://arxiv.org/abs/2406.11944) or [Marks et al.](https://arxiv.org/abs/2403.19647) and explicitly showing that JSAEs give better or clearer insights would significantly strengthen your argument. Or, pick a task where MLPs matter like the greater-than task from [Hanna et al.](https://arxiv.org/abs/2305.00586) and concretely show how JSAEs provide new insights or clearer interpretations.
3. Also, the paper would greatly benefit from more qualitative analysis. Right now, the argument primarily relies on summary statistics, which can obscure what's actually happening underneath. It would help if you showed the correlation or cosine similarity between transcoder latents and output JSAE latents, or between JSAE and normal SAE latents. Are these methods capturing similar concepts but with slightly different directions, or is the JSAE method genuinely capturing fundamentally different computations to achieve sparse Jacobians?
4. Another concern is about potential pathologies: [Lindsey et al.](https://transformer-circuits.pub/2024/crosscoders/index.html) demonstrated substantial redundancy and showed concept directions in the residual stream shifting pre- and post-MLP. My hypothesis is that this occurs because MLPs have a significant first order linear component that explains a fair amount of the variance in the output. Consequently, if this is true, achieving a sparse Jacobian might just reflect input and output SAEs capturing essentially the same concepts, with the MLP performing a simple linear transformation between them. This would result in a clean and sparse Jacobian, especially if the input features are nearly orthogonal. However, this scenario would not be particularly interesting or insightful.
5. A suggestion for improving this approach: inspired by [skip transcoders](https://arxiv.org/abs/2501.18823), if part of the issue is the MLP's output having a large linear component, why not explicitly train a linear approximation, subtract it off, and then apply your JSAE to the nonlinear remainder? This way, your Jacobian sparsity would more meaningfully represent non-linear computations rather than simple linear mappings. This might also simplify interpretation, as a purely linear output essentially extends the input SAE, which isn't particularly interesting and wastes capacity in the output SAEs.
6. Another concern: the paper implicitly mixes two distinct notions of sparsity—local sparsity (how each concept affects each output on a single prompt) and global sparsity (connections existing across all prompts). You might have an output latent activated by many different input latents but on any given prompt only fires due to a single input latent as they're all anti-correlated. Locally, that's sparse, but globally, it's dense. Currently, the paper only looks at sparsity on individual prompts. It would be helpful to see global statistics—for instance, looking at multiple prompts and measuring the probability that a given edge exists conditional on the output latent activating, then assessing sparsity at this global scale. My intuition is that it might still be somewhat sparse globally, but clarifying and verifying this explicitly is worthwhile.
## Minor Comments
*The following are unlikely to change my score, but are comments and suggestions that I hope will improve the paper, and I leave it up to the authors whether to implement them. No need to reply to all of them in the rebuttal*
1. I do like the trick used for efficiently computing Jacobians as a proxy for sparse computational graphs. It's clever and seems to be executed effectively.
2. Only studying GELU MLPs is somewhat limiting, as gated MLPs are now the standard, so this work is not directly applicable to modern LLMs. While your methods should transfer fine (albeit with more complicated derivative calculations), adding an appendix discussing this extension would help make the paper feel more complete.
3. Regarding your mention of feature absorption in the intro, it's not clear at all that JSAEs address this issue effectively. When concepts consistently co-occur, like "elephant" and "starts with E," they typically merge into something like "starts with E but isn't elephant." I don’t see why this would differ significantly in JSAEs. If this isn't a key claim, it might be better either to justify it clearly or just cut it.
4. The summary statistics about relationships between input/output latents have an unclear relationship to linearity. Since near-zero Jacobian values imply trivial linearity, it would help to filter first for active edges to better highlight meaningful relationships. The paper mentions that 88% of relationships are linear, but it isn't clear whether this percentage is notably high or low since I don't have good context for these numbers. Clarifying whether this is good or bad and providing context for this number by comparing to eg the fraction of trivial entries in the Jacobian, would significantly help interpretation.
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your careful and considered review!
### 1. Transcoders vs JSAEs
A few days ago, Anthropic published a huge new paper on circuit tracing, and which cites our work [1].
The key idea in our work and [1] is:
* Take multiple layers in network.
* Decompose each layer into sparse latents (we use SAEs at different layers, [1] uses transcoders at different layers).
* Take the Jacobian for the mapping from sparse latents at one layer to sparse latents at later layers.
* Identify strong connections using large elements in that Jacobian.
* Interpret those connections (which is much _much_ easier if the connections are sparse).
Our insight is that in any such approach, the Jacobians are denser than they could be because we don't have an efficient loss term that explicitly encourages Jacobian sparsity.
We introduce such a loss term.
Of course, the most natural place to apply such methods is to SAEs at different points in the network, as we did in our paper.
But you could equally extend our idea of sparsifying Jacobians to the transcoders at different layers in [1] to get even sparser, more interpretable circuits.
> The input vector of a transcoder latent can be projected onto a normal residual SAE's decoder to see which concepts are used, though perhaps that would have too much interference?
We agree you could do this, but based on our results, we would expect that the resulting projection would be dense, (or at least denser than it could be) and therefore difficult to interpret. We will check for the camera-ready.
[1] www.transformer-circuits.pub/2025/attribution-graphs/methods.html
### 2. Toy tasks
We have not been able to run toy tasks during the short rebuttal period, but will explore this for the camera-ready.
### 3. Qualitative results
We have updated the manuscript with qualitative [results](https://anonymous.4open.science/r/jacobian-saes-icml-D7BF/jacobian-saes-icml-examples.pdf). Specifically, we plot max-activating examples for an output feature, and the 16 input features that connect to it most strongly. The very first output latent (34455) in that document that activates fairly generally on German text. The input latents respond to:
* Tokens that frequently appear in German text. There is an input responding "Pf", another responding to "sch", and another responding to "Kle".
* "German"
* "von"
* Place names such as "Austria" and "Berlin"
There are also far more subtle examples, such as output latent 52843 (easiest to Ctrl-F). This latent is activated by "go" and "goes" in different figurative contexts, including "go on record" and "go behind his back"; it does not appear to respond to the literal meaning of movement through space. This distinction may be part of what this circuit is designed to clarify. One of the corresponding inputs include measure of extent and distance, like "a long way" and "right to the 6 th floor" and another to the word "back" in "go back". Other input latents include "go" in a figurative context, or words that have a similar role to "go" such as "proceed", "headed" and "come" and even one responding to "GO" or "GOTO" in computer code.
Note that the output features are not hand-picked, but are ordered starting with the output with the largest element of the Jacobian averaged across all inputs.
It's important to highlight that, as far as we can see, you could not get this kind of insight using transcoders of standard SAEs. Our qualitative results show that the MLP computes its output feature using _a specific set of input features_; transcoders and standard SAEs do not attempt to locate the input features used to compute a specific output feature.
### 4. Pathologies
The qualitative examples above usually show one input feature that's similar, but a lot of other input features that are different. So the pathology you are suggesting does seem to occur, but it doesn't seem to obscure other interesting patterns.
### 5. Skip transcoders
This is a great idea! This is definitely worth trying to see whether it makes things more interpretable. We will run analysis for the camera-ready deadline.
### 6. Sparsity
We agree that our current manuscript could be clearer on this point and we will clarify it in the camera-ready! We did check the global sparsity levels and your intuition is correct, it is indeed quite sparse globally. We will include data on this in the camera-ready.
### Gated MLPs
We've already worked out the math for this and will add an Appendix with experiments for the camera-ready
### Feature absorption
We have cut the claim
### Linearity
Agreed, we will add this nuance
### Conclusions
Thank you for your extensive and excellent comments! Given the number of great suggestions you made, we hope you will forgive the need to explore several points in the camera-ready deadline. If this response (especially the new qualitative results) has nonetheless addressed your key concerns, we would greatly appreciate it if you would reconsider your score.
---
Rebuttal Comment 1.1:
Comment: Thanks to the authors for their rebuttal. The qualitative data makes me much more reassured that the Jacobian SAEs are finding something genuinely interesting and interpretable, and I agree that this is meaningfully different from what standard transcoders can achieve. I would be excited to see the work applied to transcoders in the camera-ready version, but I understand this is unreasonable to expect within the rebuttal period. I also find the argument for how this could be applied to transcoders compelling and it makes me less concerned that there is insufficient value added on top of transcoders, since the techniques can be combined. Given both of these factors, I am increasing my score from 3 to 4. | Summary: This work introduces Jacobian Sparse Autoencoders (JSAEs), an extension of sparse autoencoders (SAEs) designed to sparsify not only latent activations but also the computational graph (approximated via the Jacobian) of an MLP layer in LLMs models.
Authors also show how to compute efficiently the Jacobian thanks to the top-k SAE approach (namely only the non-zero parts are computed), encouraging the Jacobian to be sparse. Their findings include:
- JSAEs significantly increase the sparsity of the Jacobian between input and output latent spaces compared to standard SAEs with minimal cost and small drop in reconstruction quality and model performance.
- Input and output latents learned by Jacobian SAEs are approximately as interpretable as standard SAEs, as quantified by auto-interpretability scores.
- When applied to randomly initialized transformers, JSAEs achieve much less Jacobian sparsity than when applied to pre-trained transformers. This suggests that Jacobian sparsity is a property of the trained model, indicating its potential as a tool to uncover learned computational structure, something latent sparsity alone may not capture.
- The function learned by the JSAE-MLP-JSAE pipeline is shown to be mostly linear, meaning the Jacobian is a reliable proxy for true computational sparsity in this context.
Claims And Evidence: Yes, claims are well-supported by both theoretical derivations and experimental evidence.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes. The setups, loss, efficient computation of Jacobian and almost linearity of $f_s$ seems correct.
Experimental Designs Or Analyses: Yes, the setting is legit. However, the paper would benefit from more qualitatevely results (i.e. the standard mechanistic approach to identify what concepts or features the model has learned).
Supplementary Material: Yes. The supplementary material includes detailed description on how to efficiently compute the Jacobian (Appendix A), almost linearity of $f_s$ (Appendix B), and additional experimental setting and results (Appendix C and D).
Relation To Broader Scientific Literature: The paper builds directly on prior work on SAEs and contributes to sparsify not only the activations but also the computational graph.
Essential References Not Discussed: Essential references are discussed. However, in Section 2 the authors should mention why SAEs are introduces in general, so the superposition hypothesis and polysemantic neurons.
Other Strengths And Weaknesses: ### Strengths
- The idea of sparsifying the computation (not just the representation) is new and compelling. It nicely bridges concepts from automated circuit discovery and dictionary learning.
- Insightful findings for discovering sparse computation in LLMs.
- The papers is really well-written and organized (yes for me it's a strenght because it's not always the case, even for top conferences).
### Weaknesses
- Lack of qualitatevely results (i.e. the standard mechanistic approach to identify what concepts or features the (J)SAEs have learned).
- JSAEs are only trained on individual MLPs. This is fine as a starting point, but the paper lacks a discussion on how to extend this to full multi-layer transformer analysis.
Other Comments Or Suggestions: Figure 1, write in the figure (not only in the caption) what $\tau_k$ is.
Questions For Authors: - Are the MLP $f$ parameters updated when training JSAEs?
- Figure 2, what is the Jacobian of traditional SAEs?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your positive review, which notes "The idea of sparsifying the computation (not just the representation) is new and compelling. It nicely bridges concepts from automated circuit discovery and dictionary learning.
Insightful findings for discovering sparse computation in LLMs.
The papers is really well-written and organized".
### Qualitative results
We have updated the manuscript with qualitative [results](https://anonymous.4open.science/r/jacobian-saes-icml-D7BF/jacobian-saes-icml-examples.pdf). Specifically, we plot max-activating examples for an output feature, and the 16 input features that connect to it most strongly. The very first output latent (34455) in that document that activates fairly generally on German text. The input latents respond to:
* Tokens that frequently appear in German text. There is an input that mainly responds to "Pf", and another that responds to "sch", and another that responds to "Kle".
* "German"
* "von"
* Place names such as "Austria" and "Berlin"
There are also far more subtle examples, such as output latent 52843 (easiest to Ctrl-F). This latent is activated by "go" and "goes" in different figurative contexts, including "go on record" and "go behind his back"; it does not appear to respond to the literal meaning of movement through space. This distinction may be part of what this circuit is designed to clarify. One of the corresponding inputs include measure of extent and distance, like "a long way" and "right to the 6 th floor" and another to the word "back" in "go back". Other input latents include "go" in a figurative context, or words that have a similar role to "go" such as "proceed", "headed" and "come" and even one responding to "GO" or "GOTO" in computer code.
Note that the output features are not hand-picked, but are ordered starting with the output with the largest element of the Jacobian across all inputs.
### Discussion of extending JSAEs to full multi-layer transformer analysis
We agree that we applied JSAEs only to locally (to individual MLPs). This mirrors many other interpretability approaches, such as:
* SAEs, which allow you to interpret the activations at a single location in the network
* transcoders, which allow you to interpret the activations again for an MLP.
The difference between JSAEs and these approaches is that there is a natural extension of JSAEs to "global interpretability". In particular, you can train SAEs at many points in the network, and minimize the Jacobian for the mappings between latent activations in these SAEs.
Indeed, we believe that this methodology could naturally be to further sparify the Jacobians between _transcoder latents_ in the fantastic work released by Anthropic only a few days ago [1].
[1] https://transformer-circuits.pub/2025/attribution-graphs/methods.html
We have added this discussion to our working draft.
> Figure 1, write in the figure (not only in the caption) what is.
Thanks! Fixed.
> Are the MLP parameters updated when training JSAEs?
No. The underlying MLP parameters are fixed to those in pre-training.
The only thing that is updated is the encoder/decoder of the SAEs.
The new thing is including a term in the loss for the encoder/decoder of the SAE which encourages sparse Jacobians when we consider the mapping from sparse inputs to sparse outputs.
> Figure 2, what is the Jacobian of traditional SAEs?
Traditional SAEs still have a Jacobian. You can still train a traditional SAE at the input and output of an MLP, then look at the Jacobian from sparse inputs to sparse outputs. The difference between an SAE and a JSAE is simply in the training objective. Specifically, the JSAE objective includes a term that encourages sparse Jacobians, while the SAE does not. As such, the SAE is also equivalent in e.g. Figure 3 to a Jacobian Loss Coefficient of zero.
### Conclusions
Thank you for generously outlining the paper's strengths in your original review. We hope this response (especially the new qualitative results) has addressed your key concerns. If so, we would greatly appreciate it if you would reconsider your score. | Summary: This paper addresses the problem of better understanding computations in deep models, particularly LLMs. Recently sparse autoencoders (SAEs) have become popular as a tool to mechanistically understand a model, by decomposing features learnt at any layer into a sparse set of disentangled concepts. This work proposes Jacobian SAE (JSAE), which aims to additionally sparsify the computations by MLP layers in LLMs, by enforcing sparsity on connections between TopK latents at the input and output of the MLP, approximated using the Jacobian. Experimental evaluation is performed to show that JSAEs can learn to reconstruct features similar to traditional SAEs while having much sparser connections for the computations between the constituent input and output SAE. Sanity test experiments are also performed to show that what is learnt is meaningful, e.g. that the sparsity is better for JSAEs trained on a learnt MLP as opposed to a randomly initialized MLP.
## Update after rebuttal
Thank you for your response, particularly for providing examples. They look quite interesting, and it would be very helpful to have more examples (or some latent exploration tool) in the final paper. Regarding the question about zeroing out connections: I actually meant something even simpler---one could pick a small threshold, e.g. 1e-4, and set any weight in the JSAE below that threshold to zero _post-hoc_, and then compute the performance, to see if the weights below the threshold are actually meaningfully important. This was intended to be more of a sanity check to verify results from Figure 3.
Overall however I believe this is an interesting and useful paper, so I would like to change my score to accept.
Claims And Evidence: Generally yes, except for concerns raised in the Weaknesses section below.
Methods And Evaluation Criteria: The method makes sense. The evaluations are reasonable but inadequate, as discussed in the Weaknesses section below.
Theoretical Claims: I looked over the claims in Appendix A and B but did not go through them in full detail. To that extent, they appear reasonable.
Experimental Designs Or Analyses: The experimental design and analyses appear sound to the extent they have been done. However, additional evaluation is needed, as discussed in the Weaknesses section below.
Supplementary Material: I skimmed over parts of the supplementary material referred to in the main text, primarily the derivations in Appendix A, and result figures such as Figure 25.
Relation To Broader Scientific Literature: This work builds upon existing literature that aims to disentangle concepts learnt by deep models such as LLMs using SAEs. However, different from typical SAEs, it also focuses on sparsifying and understanding the computations in the LLM and not just features at a given layer. This is similar to the idea of transcoders, but not identical, as discussed in Section 2.2.
Essential References Not Discussed: None that I am aware of.
Other Strengths And Weaknesses: ## Strengths
1. The paper looks into an interesting and potentially useful problem, of understanding computations made by large models, as opposed to just examining what features were learnt as is typically done with SAEs.
2. The proposed idea of learning sparse connections using the Jacobian is interesting and appears to be novel.
3. Experimental evaluation shows that the learnt JSAEs perform comparably to traditional SAEs while also being significantly sparser.
4. The paper is generally well written and easy to follow.
## Weaknesses
1. The biggest weakness is that there does not seem to be any example of a use case of such JSAEs. In typical SAEs, one can see examples of latents learning human interpretable features, along with evaluations, both qualitative and quantitative, to show that they are (for the most part) disentangled and meaningful (e.g. Bricken et al. 2023, Bills et al. 2023). Evaluations also often show downstream uses such as model steering. However, this work does not have any indication on what JSAEs could be used for at all. Since the stated motivation is to learn a sparse mapping between SAE concepts before and after an MLP, it would be critical to see what this learnt mapping actually encodes, particularly since the point of training such SAEs is to aid human interpretability. At the very least, one should have qualitative examples of concepts at the input, output, and weights connecting them, and ideally have a more thorough quantitative analysis.
2. The sparsity of JSAEs is shown by thresholding weights and counting how many are above the threshold. However, it is possible that the weights below this threshold still contribute meaningfully—it would be make more sense to evaluate reconstruction quality by explicitly zeroing out everything below the threshold and then computing the metrics in Figure 3. This would after all be the likely practical use of such trained JSAEs.
Other Comments Or Suggestions: - L048: $L^1 \to L_1$
Questions For Authors: Please refer to the Weaknesses section. While the idea and approach appear interesting, in particular Weakness 1 is a critical omission and needs to be addressed. Any discussion on this in the rebuttal would be helpful.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review, noting "(1) The paper looks into an interesting and potentially useful problem, of understanding computations made by large models, as opposed to just examining what features were learnt as is typically done with SAEs. (2) The proposed idea of learning sparse connections using the Jacobian is interesting and appears to be novel. (3) Experimental evaluation shows that the learnt JSAEs perform comparably to traditional SAEs while also being significantly sparser. (4) The paper is generally well written and easy to follow."
### Qualitative results
We have updated the manuscript with qualitative [results](https://anonymous.4open.science/r/jacobian-saes-icml-D7BF/jacobian-saes-icml-examples.pdf). Specifically, we plot max-activating examples for an output feature, and the 16 input features that connect to it most strongly. The very first output latent (34455) in that document that activates fairly generally on German text. The input latents respond to:
* Tokens that frequently appear in German text. There is an input that mainly responds to "Pf", and another that responds to "sch", and another that responds to "Kle".
* "German"
* "von"
* Place names such as "Austria" and "Berlin"
There are also far more subtle examples, such as output latent 52843 (easiest to Ctrl-F). This latent is activated by "go" and "goes" in different figurative contexts, including "go on record" and "go behind his back"; it does not appear to respond to the literal meaning of movement through space. This distinction may be part of what this circuit is designed to clarify. One of the corresponding inputs include measure of extent and distance, like "a long way" and "right to the 6 th floor" and another to the word "back" in "go back". Other input latents include "go" in a figurative context, or words that have a similar role to "go" such as "proceed", "headed" and "come" and even one responding to "GO" or "GOTO" in computer code.
Note that the output features are not hand-picked, but are ordered starting with the output with the largest element of the Jacobian averaged across all inputs.
### Zeroing-out connections with small Jacobians
There are two different kinds of zeros in our Jacobians.
* First, there are zeros in the Jacobian that arise due to most of the inputs and outputs being ``off'', as they are zeroed out by the k-sparse SAEs. This sparsity is already accounted for in the reconstruction errors in the main text.
* Second, there are small elements of the Jacobian even where the input and output features are on.
Given our overall approach, this second kind of sparsity in the Jacobian is very difficult to zero-out.
We chose a particular approach which has many advantages, but sadly does not allow for an analysis such as this.
Specifically, we needed to choose between two potential approaches:
* You could compute the Jacobian of the \textit{actual} MLP in the underlying network. This has the critical advantage of having no approximation error, as it is working with the Jacobian of the actual MLP.
* You could train a function with a simple/sparse Jacobian to approximate the input/output behavior of the MLP. This has the disadvantage that there is now approximation error. But on the other hand, this function can designed to be manipulated more easily.
We chose the first approach, as it removes a source of approximation error (from the function you've trained to approximate the MLP). But it does mean that you can't zero-out an element of the Jacobian, because this is the Jacobian of the underlying MLP, and we don't know how to zero-out elements of a Jacobian from a complex MLP. The second approach would allow for this, and we intend to investigate it in future work.
> $L^1 \rightarrow L_1$.
Thanks! Fixed.
### Conclusions
Thank you for generously outlining the paper's strengths in your original review.
We hope this response (and especially the new qualitative results) has addressed your key concerns.
If so, we would greatly appreciate it if you would reconsider your score. | null | null | null | null | null | null |
Privacy Amplification Through Synthetic Data: Insights from Linear Regression | Accept (poster) | Summary: The paper offers a theoretical analysis of the privacy loss of releasing synthetic samples in linear regression. It demonstrates that, under a strong threat model where an adversary controls the seed of the generative model, releasing even a single synthetic sample can result in privacy leakage equivalent to that of releasing the full generative model in the worst case. Conversely, when the seed is random, the authors prove a form of privacy amplification.
Claims And Evidence: There are a couple of points that I find problematic or unclear:
- "It is clear that the adversary can recover the model parameters $v^*$ from $d$ queries...Strikingly, we now show that the
adversary can in fact recover the model parameter with just one query." --> The discussion here is very confusing. Privacy leakage is not about recovering model parameters (as a matter of fact, they are already known after training), but rather about inferring information about the training samples. Additionally, what you really show here is that with one query it is possible to achieve the maximum privacy leakage (as specified by the privacy budget of training the generative model) for some worst-case datasets.
- "Since Label DP is a weaker notion than standard DP, these results also imply negative results for standard DP" --> I don't follow this claim. How does a construction where releasing a single synthetic sample achieves maximum privacy leakage under Label DP translate into a construction for standard DP?
- "However, these results do not imply that for every possible seed $z$, the privacy loss $T(V_\infty z, W_\infty z)$ is strictly smaller than $T(V_\infty, W_\infty)$" --> I'm confused about this argument. Mathematically, it seems to be the case that $\|A\Sigma X^\top (y_i-y_i')\| \le \|A X^\top (y_i-y_i')\|$ does not necessarily hold. On the other hand, the post-processing property of DP guarantees that the privacy loss of releasing a single data point is upper bounded by the privacy loss of training the generative model. How can these two observations be reconciled?
Methods And Evaluation Criteria: N/A
Theoretical Claims: - For output perturbation, Chaudhuri et al., 2011 assumes certain properties of the loss function, specifically bounded gradient (or equivalently, Lipschitz), to upper bound the L2 sensitivity of the minimizer of the regularized least-square objective. To satisfy this property, they primarily focus on classification losses such as cross-entropy and hinge loss and assume that the samples have bounded norm. In contrast, the current paper directly borrows the results from Chaudhuri et al., 2011 but applies them to linear regression. The assumptions from Chaudhuri et al., 2011 are not formally stated, and the gap between the two settings is not addressed, which is problematic. In fact, the gradient of the square loss is not necessarily bounded without additional assumptions.
- The authors claim that "As a discretized Langevin dynamical system with a convex objective, it is known that $V_t$ converges in distribution to its stationary Gibbs distribution". This claim is made without any references or citations. My understanding is that while Langevin dynamics with a convex objective do converge to the stationary Gibbs distribution in continuous time, this convergence is not guaranteed for discretized processes without further assumptions on the step size. This lack of rigor is concerning.
Experimental Designs Or Analyses: N/A
Supplementary Material: I checked Appendix A but did not read Appendix B in detail. The proofs generally make sense to me. Minor: in the proof of Proposition A.5, sigma --> \sigma.
Relation To Broader Scientific Literature: The paper contributes to the literature on DP data synthesis by providing a formal analysis of the privacy loss of synthetic samples. It also extends the literature on privacy amplification by identifying an alternative mechanism---privacy amplification through synthetic data---beyond traditional approaches such as subsampling and iteration, once again showcasing the power of randomness in privacy protection.
Essential References Not Discussed: For DP synthetic data generation, the authors should discuss [1]. In particular, Figure 1 offers a useful overview of the current state of the field.
At a high level, the phenomenon uncovered in this work resembles privacy amplification by iteration: releasing only the final model checkpoint, rather than all the intermediate ones, leads to better privacy. In addition to Feldman et al., 2018, the authors should consider discussing [2,3,4], which provide last-iterate privacy analysis under the assumptions that the loss function is convex and/or smooth, showing that the privacy loss is bounded as $T$ goes to infinity. Moreover, it would be beneficial to review several works on privacy amplification by subsampling [5,6]. Collectively, these studies highlight the power of randomness in privacy protection.
[1] Hu, Yuzheng, et al. "Sok: Privacy-preserving data synthesis." 2024 IEEE Symposium on Security and Privacy (SP). IEEE, 2024.
[2] Altschuler, Jason, and Kunal Talwar. "Privacy of noisy stochastic gradient descent: More iterations without more privacy loss." Advances in Neural Information Processing Systems 35 (2022): 3788-3800.
[3] Ye, Jiayuan, and Reza Shokri. "Differentially private learning needs hidden state (or much faster convergence)." Advances in Neural Information Processing Systems 35 (2022): 703-715.
[4] Chien, Eli, and Pan Li. "Convergent privacy loss of noisy-sgd without convexity and smoothness." arXiv preprint arXiv:2410.01068 (2024).
[5] Balle, Borja, Gilles Barthe, and Marco Gaboardi. "Privacy amplification by subsampling: Tight analyses via couplings and divergences." Advances in neural information processing systems 31 (2018).
[6] Steinke, Thomas. "Composition of differential privacy & privacy amplification by subsampling." arXiv preprint arXiv:2210.00597 (2022).
Other Strengths And Weaknesses: Strengths: The paper provides, to the best of my knowledge, the first theoretical analysis of the privacy loss of the synthetic samples generated by DP-trained generative models. Although the setting appears somewhat toyish, the techniques employed, particularly for releasing multiple points, are non-trivial. Overall, this work could serve as a promising first step toward an important research direction.
Weaknesses: The main factor lowering my overall rating is related to the theoretical claims; I feel that the rigor in this work does not meet the bar for ICML. Additionally, the paper could be strengthened by:
- Including a notation section. For instance, $||\cdot||$ is typically interpreted as the 2-norm, but here it is mostly used as the Frobenius norm. Moreover, $\delta_{ij}$, which appears in both Sec 3.1 and Prop 4.2, is never formally defined.
- Providing an overview of the proof techniques. It would be helpful to discuss the technical challenges and how the paper addresses them.
- Discussing the implications of the main results. For example, how does Theorem 4.8 relate to privacy amplification? What is the relationship between $\tilde{G}_{\Lambda(\sigma_w, d, \Delta)}$ and $T(V,W)$?
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank Reviewer pnmm for providing valuable feedback and pointing out several valid issues. Below, we address and discuss each point.
## Claims And Evidence
> Privacy leakage is not about recovering model parameters
We agree that our sentence might be confusing. What we mean here is that if the adversary is able to recover the model parameters, then no privacy amplification is possible compared to the privacy guarantee given by post-processing the model (this is what we call "maximum privacy leakage" in this context). We show that a single query is sufficient for an adversary to achieve this maximum privacy leakage (Proposition 3.1).
> How… Label DP translate into a construction for standard DP
DP upper bounds the privacy leakage across all possible pairs of adjacent datasets. In Label DP, adjacent datasets differ only in their labels. Since any two datasets that are adjacent under Label DP remain adjacent under standard DP (where both features and labels can differ), a lower bound on the privacy leakage in the Label DP setting also applies to standard DP.
> Mathematically, it seems to be the case that $|A\Sigma X^T(y_i'- y_i)| \leq |A X^T(y_i'- y_i)|$ does not necessarily hold
You are right, thanks for catching this. There is a minor error in the upper bound. We address this in the "Theoretical claims" section below, where you also raised a related question about the convergence of NGD.
## Theoretical claims
> Output perturbation is not possible without Lipschitz condition on the objective function
You are right and we thank you for pointing out this oversight. To ensure the loss is Lipschitz, we can assume that $\|x\| \leq M_x, \|y\| \leq M_y$ and limit the parameter space to the centered ball of radius $M_\theta$ (the latter condition is always verified for ridge regression). Such conditions are common in private linear regression analysis, see for e.g. [1]. The objective is then $L$-Lipschitz with $L = M_x^2 M_\theta + M_x M_y + \lambda M_\theta$, allowing us to use the output perturbation mechanism and to keep our results unchanged.
[1] Y. X. Wang. Revisiting differentially private linear regression: optimal and adaptive prediction & estimation in unbounded domain. AISTATS 2018.
> Discrete convex Langevin dynamical systems do not necessarily converge
Again, you are right. The ergodicity of the process is required for convergence, and is ensured when the objective function is strongly convex and smooth (see for e.g., [2]), which is the case in our setting. Furthermore, for NGD with full batch training, it can be shown that if the learning rate $\eta$ is sufficiently small, then $V_t$ converges to a normal distribution, which is the Gibbs distribution when $\eta \to 0$. The correct result writes as follows.
>Let $\Sigma = \frac{1}{n}X^T X + \lambda I$, $M = I - 2\eta\Sigma$ and denote by $A$ the square root of $\Sigma^{-1} M$. Without loss of generality, assume that $y$ and $y'$ differ. Assume that $\eta(\lambda + M_x^2/n) <1$. Then:
$$T(V_\infty,W_\infty) = G_{\sqrt{2}\|A X^T (y-y')\|/n\sigma}.$$
Moreover, for two given datasets, the adversary can choose $z \in \mathbb{R}^d$ such that:
$$T(V_\infty z,W_\infty z) = G_{\sqrt{2}|\sigma_{\max}(A X^T (y-y'))|/n\sigma}.$$
In particular, if $y'$ and $y$ are adjacent (label DP), the adversary can choose $z \in \mathbb{R}^d$ such that:
$$T(V_\infty z,W_\infty z) = T(V_\infty,W_\infty).$$
This result corrects both the confusion about convergence of $V_t$ and Propositions 3.2 to 3.4.
Due to space limitations, we are not able to give the sketch of proof here, but we are happy to provide it as a follow-up comment to the reviewer.
[2] A. Durmus, S. Majewski, and B. Miasojedow. Analysis of Langevin Monte Carlo via convex optimization. J. Mach. Learn. Res. 20:73, 2019
## References not discussed
Thank you for highlighting these references. We will add a citation to this recent survey and discuss how our work relates to other privacy amplification results. As you noted, synthetic data release is a distinct phenomenon that extends beyond privacy amplification by iteration. In the latter, the final model is released at the end of private training, while our approach further conceals the model itself and discloses only synthetic data generated from random inputs to the model.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response. I am raising my score to 3 due to the authors’ efforts in improving the rigor of the paper.
---
Reply to Comment 1.1.1:
Comment: We thank Reviewer pnmm for raising their score. For completeness, we include a sketch of proof of corrected Propositions 3.2 to 3.4, as outlined in our rebuttal.
### Proof of corrected Propositions 3.2 to 3.4
We consider NGD with the following update: $V_{k+1}^T = V_k^T - \frac{1}{n}\eta \sum_{i=1}^m \nabla_w f(V_k^T,x_i,y_i) + \sqrt{\eta} N_{k+1}$. Note that we changed the scaling of $\eta$ for the noise in order for our results to hold. The gradient is $\sum_{i=1}^m \nabla_w f(V_k^T,x_i,y_i) = X^T(XV_k^T - y) + \lambda V_k^T$. Then, noting $B = \frac{2\eta}{n} X^T y$, we get $V_{k+1}^T= MV_k^T + B + \sqrt{\eta} N_{k+1}$.
Then,
$$V_t^T = M^t V_0^T+ \sum_{k=0}^{t-1} M^{t-1-k} (B + \sqrt{\eta} N_{k+1}),$$
which is composed of independent columns with mean $\mu^i_t = (I-M)^{-1}(I - M^t)B_i$ and covariance $\Sigma^i_t = M^{2m} + \eta \sigma^2 (I - M^2)^{-1}(I-M^{2t})$. Assume that $\eta(\lambda + M_x^2/n) < 1$.
Then $M^t \to 0$ and:
$$\mu^i_t \to (I-M)^{-1}B_i = \frac{1}{n}\Sigma^{-1} X^T y_i,$$
$$\Sigma^i_t \to \eta \sigma^2 (I - M^2)^{-1} = \frac{\sigma^2}{2}(I-2\eta\Sigma)^{-1}\Sigma^{-1} = \frac{\sigma^2}{2}M^{-1}\Sigma^{-1}.$$
By Levy's continuity theorem, $V_t \to V_\infty \sim N( \Sigma^{-1} X^T y/n, \sigma^2 M^{-1} \Sigma^{-1}/2 \otimes I_n)$ (there is an abuse of notation here because we use the vectorized notation). Note that when $\eta \to 0$, we recover the Gibbs distribution.
We note $B^2 = \Sigma^{-1} M^{-1}$. The square roots are defined because $\Sigma$ and $M$ commute.
By Lemma A.2, the tradeoff function between $V_\infty$ and $W_\infty$ is $T(V_\infty,W_\infty) = G_{\sum_{i=1}^n ||\mu_i'-\mu_i||_{2M\Sigma/\sigma^2}}$, with $\mu_i' = \frac{1}{n}\Sigma^{-1}X^Ty_i', \mu_i = \frac{1}{n}\Sigma^{-1}X^Ty_i$, and:
$$||\mu_i'-\mu_i||_{2M\Sigma/\sigma^2}^2 = (y_i'-y_i)^T X \Sigma^{-1} M X^T (y_i'-y_i)/\sigma^2 = 2||AX^T(y_i'-y_i)||^2/n^2\sigma^2.$$
Furthermore, for $z \in \mathbb{R}^d$, $V_\infty z \sim N((\Sigma^{-1} X^T y_i \cdot z)_i/n, \sigma^2 z^T M^{-1} \Sigma^{-1}z I_n/2)$,
Then, $$T(V_\infty z,W_\infty z) = G_{\frac{\sqrt{2}||z^T \Sigma^{-1} X^T (y-y')||}{ n\sigma || B z||}}.$$
By noting the change of variable $u = Bz$ and using the invertibility of $B$, we get:
$$\sup_{z \neq 0} \frac{||z^T \Sigma^{-1} X^T (y-y')||}{ || B z||} = \sup_{u \neq 0} \frac{||u^T (A X^T (y-y'))||}{ ||u||} = \sigma_{\max}(A X^T (y-y')),$$ which corresponds to the 2-norm of $AX^T(y-y')$ and is obtained by setting $u^*$ the right singular vector corresponding to the largest singular value of $A X^T (y-y')$. In the setting of Label DP, $y'-y$ has rank $1$, so $T(V_\infty z,W_\infty z) = T(V_\infty,W_\infty)$. | Summary: This paper investigates privacy amplification from synthetic data release within the specific setting of linear regression.
The authors first establish negative results, showing that an adversary controlling the seed of the generative model can induce the maximum possible privacy leakage from a single query.
Conversely, they demonstrate that generating synthetic data from random inputs amplifies privacy beyond the model's inherent guarantees when releasing a limited number of synthetic data points. The amplification holds in the regime when few synthetic samples are released and the ambient dimension d is large.
This highlights the crucial role of randomization in the privacy of synthetic data generation.
---
## update after rebuttal
The paper presents an interesting theoretical observation, which I appreciate, albeit with limited potential applications. The rebuttal reinforces my stance.
Claims And Evidence: The theoretical claims are supported by proofs.
Methods And Evaluation Criteria: N/A
Theoretical Claims: I briefly checked the proofs but not in thorough detail.
Experimental Designs Or Analyses: N/A
Supplementary Material: I reviewed the proofs in the appendix but not in thorough detail.
Relation To Broader Scientific Literature: The key contribution is the formal proof that releasing synthetic data can in fact reduce privacy loss compared to releasing a privatized model. This is in contrast to most prior works where the privacy loss is bounded using post-processing once there is a privately learned generative model. While privacy amplification from synthetic data is not completely new, past works only study the simpler case of univariate Gaussian data (Neunhoeffer et al., 2024).
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- This work provides a decently thorough examination of privacy amplification from synthetic data release in the setting of linear regression, including an impossibility result when the internal randomness of the generator is controlled by an adversary, and a positive result when the internal randomness is actually random.
Weaknesses:
- The amplification only holds when the number of generated points is less than the dimension. However, we need $O(d)$ samples to learn the parameters of a linear model, so it doesn't seem possible to learn the linear model using synthetic data while satisfying privacy amplification.
- Another potential weakness is the limitations of the model as well as techniques, which are unlikely to extend beyond linear regression to, e.g. neural networks, where synthetic data is much more useful.
That being said, I believe the theoretical results are interesting within their scope and can be a plausible addition to ICML.
Other Comments Or Suggestions: It might be helpful to contextualize the amplification results in terms of (eps, delta)-DP, perhaps even in restricted choices of the parameters, to better interpret the quantitative improvement over simple post-processing.
Questions For Authors: 1. Are there any downstream applications the authors envision for releasing $< d$ private synthetic data points from a linear model?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank Reviewer ukYX for their feedback. Below, we address each concern separately.
## Weaknesses
> The amplification only holds when the number of generated points is less than the dimension
This is correct. However, our results do not imply that privacy amplification does not happen when the number of generated points is larger. Our work focuses on the theoretical existence of privacy amplification by synthetic data release. Making it more generally applicable is an interesting open problem.
> "... limitations of the model as well as techniques, which are unlikely to extend beyond linear regression"
We agree that the generalization of our results to deeper models present significant challenges. However, we believe our findings have the potential to be leveraged in broader settings. For instance, the post-processing theorem ensures that the results also apply to regression problems with activation functions---such as logistic or ReLU regression---provided that Lipschitzness and convexity are preserved.
A promising direction for broader applicability is private fine-tuning of the last layer in deeper neural networks, which maintains the linear regression framework. However, modeling the distribution of the noise in this setting becomes more challenging, as the transformation of the Gaussian input through the layers alters its statistical properties. We leave this exploration for future work.
## Questions
> "Are there any downstream applications the authors envision for releasing $\leq d$ private synthetic data points from a linear model?"
As you pointed out in your comment, revealing less than $d$ synthetic data points has limited utility. However, our work is the first to highlight scenarios where amplification is provable, laying the groundwork for deeper theoretical exploration in broader, more realistic contexts. We are confident that our privacy bounds can be extended in practical settings. This is an objective for future work. | Summary: This paper explored the privacy amplification properties of hiding the generative model in private synthetic data generative contexts. Differentially private generative models produce synthetic data that formally inherits the same privacy guarantees. In practice, it has been observed that when the synthetic data generated is small enough, it meets stronger guarantees than the generating model, through an amplification effect. This paper formally shows that this amplification effect exists in cases where synthetic data is generated from random inputs to private linear regression models as case study. In particular, releasing synthetic data leads to stronger privacy guarantees than releasing the generative models when the number of released samples is small enough. The paper also demonstrates that in the case where the adversary has access to the seed of the generative algorithm, there is no such amplification of privacy.
Claims And Evidence: The claims in the paper are well supported by theorems, propositions and lemmas. I reviewed the theoretical results in the main paper, which appear well structured and correct. I did not review proofs and other results in the Appendix.
Methods And Evaluation Criteria: The goal of the paper is to provide an initial theoretical framework to study the phenomenon of privacy amplification through synthetic data. This is achieved mainly via theoretical analysis that is appropriate with respect to the overall goal.
Theoretical Claims: I checked all proofs and results in the main text, and to the best of my knowledge they seem correct. I did not however have the time to review results in Appendix.
Experimental Designs Or Analyses: N/A
Supplementary Material: No, I did not review the Appendix for time constraints.
Relation To Broader Scientific Literature: The main contribution of the paper is to set up the theoretical framework to study privacy amplification via synthetic data, a phenomenon that was empirically highlighted in work by Annamalai et al. (2024), and in part explored by Neunhoeffer (2024) in a more limited context where training data is one-dimensional and the generative model is a Gaussian with mean and variance estimated privately from the data. This paper uses linear regression to study the phenomenon in a more extended way. The contribution is two-fold: i) the author(s) first prove a negative result: for both output perturbation and noisy gradient descent as methods to privately train the generative model, releasing synthetic data from fixed inputs does not lead to privacy amplification (Theorem 3.1 and 3.4 respectively); ii) then, the paper proves privacy amplification for the single release case (Theorem 4.8) and the more general case of multiple releases (Theorem 4.11). To the best of my knowledge, these contributions are novel, and pave the way for new valuable results in this line of research.
Essential References Not Discussed: I don't think any essential related work was left out of the discussion.
Other Strengths And Weaknesses: Strengths:
- The paper addresses an important open question by developing a theoretical framework for quantifying privacy guarantees in synthetic data release, specifically in the context of linear regression. This rigorous approach helps fill a gap in understanding privacy amplification in generative models.
- The paper presents both positive and negative results. It demonstrates that privacy amplification is possible under certain conditions (with random inputs) while also highlighting scenarios where the privacy benefits don't hold, such as when an adversary controls the synthetic data generation seed.
Limitations:
- Restricting the focus to linear regression provides a clean case study but limits the generalizability of the findings: it’s unclear how well these results could extend to more complex models.
- As stated by the author(s), while these findings lay the ground for better insights into private synthetic data, their practical impact is limited.
Other Comments Or Suggestions: No additional comments or suggestions at the moment.
Questions For Authors: No specific questions at the moment.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer c2xJ for their interesting and positive feedback. Below, we address each concern separately.
## Limitations
> Restricting the focus to linear regression provides a clean case study but limits the generalizability of the findings: it’s unclear how well these results could extend to more complex models.
We agree that the generalization of our results to deeper models present significant challenges. However, we believe our findings have the potential to be leveraged in broader settings. For instance, the post-processing theorem ensures that the results also apply to regression problems with activation functions---such as logistic or ReLU regression---provided that Lipschitzness and convexity are preserved.
A promising direction for broader applicability is private fine-tuning of the last layer in deeper neural networks, which maintains the linear regression framework. However, modeling the distribution of the noise in this setting becomes more challenging, as the transformation of the Gaussian input through the layers alters its statistical properties. We leave this for future work. | Summary: This paper investigates the privacy amplification effect that could be gained when hiding the model that has been used to generate differentially-private synthetic data. The objective is to be able to quantify the privacy gain obtained by releasing only a limited number of synthetic data and not the model itself. More precisely, the authors show that releasing a number of synthetic profiles smaller than the input dimension provides strong privacy guarantees.
Claims And Evidence: Currently, the paper does not contain any experiments for validating the theoretical claims made. If possible, it would have been great to conduct some auditing experiments on controlled datasets to be able to verify these claims.
Methods And Evaluation Criteria: The paper takes a novel approach of trying to model the worst-case approach for the generative process by giving the control of the seed to the adversary. While this approach is promising, there is however no experimental methodology proposed for validating the performance of such adversarial approach in practice.
Theoretical Claims: The theoretical claims are made with respect to two different variants of differential privacy, namely f-DP and Rényi DP. Ideally, it would have been great if the authors could have elaborated on why such notions are necessary compared to the classical DP definition.
Nonetheless, the authors have been able to show that in the specific case of differentially-private linear regression, there exists situation in which if the adversary is able to manipulate the randomness used by the generative process, he can achieve the theoretical upper bound in terms of privacy leakage.
To be frank, the proofs are highly technical and specialized and I do not have the expertise to validate them thoroughly.
Experimental Designs Or Analyses: The theoretical analysis seem sound although as mentioned earlier I do not have the technical expertise to validate them fully. However, there is no experiments set up for validating them.
Supplementary Material: I have reviewed the supplementary material, however as mentioned previously the proofs in appendices are technically heavy and I do not have the expertise to thoroughly validate them.
Relation To Broader Scientific Literature: The main results of the paper contributes to better understand the privacy guarantees that are possible in a context in which only synthetic data is released and not the model itself. However, the impact is limited in the sense that the results only holds if the number of released synthetic samples is very small compared to the input dimension, which is very limited in terms of practical interests.
Essential References Not Discussed: I do not see any missing important references, rather the authors have done a good job at reviewing the corresponding state-of-the-art.
Other Strengths And Weaknesses: The paper is well-written and the authors have done a good job at explaining the current state-of-the-art on the evaluation of DP guarantees of synthetic data. The theoretical analysis conducted is interesting but only holds for a very small release of synthetic data and thus I consider that the term "privacy amplification" used in the title is exaggerated. There is also a lack of experiments to validate practically the theoretical claims.
Other Comments Or Suggestions: A small typo : « Without loss of generarilt » -> « Without loss of generality »
Questions For Authors: It would be great if the authors could comment on the potential of the approach to generalize to other types of models.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank Reviewer RSvt for their feedback. Below, we address each concern separately.
## Weaknesses
> The term "privacy amplification" used in the title is exaggerated
In our paper, the phrase "privacy amplification from synthetic data release" refers to potential privacy gains achieved by releasing only synthetic data while keeping the generative model hidden. We demonstrate that this privacy amplification does not occur when the adversary controls the seed. However, existing empirical studies suggest the existence of this effect when the seed is randomized (e.g., [1]). This empirical observation motivates our research question: *Can privacy amplification occur from synthetic data release, or are existing membership inference attacks simply insufficiently powerful to achieve the maximal privacy leakage?*
To address this, we conduct a rigorous theoretical analysis in a simplified linear regression setting. Our results are the first to show that under certain conditions, privacy amplification can indeed occur—even achieving perfect privacy as $d$ increases. While our analysis applies to a specific setting, it does not rule out amplification in more general cases. Instead, our work highlights scenarios where amplification is provable, laying the groundwork for deeper theoretical exploration in broader, more realistic contexts. This motivation is reflected in our title: "Insights from linear regression".
[1] Annamalai, M. S. M. S., Ganev, G., and Cristofaro, E. D. "What do you want from theory alone?" Experimenting with tight auditing of differentially private synthetic data generation. USENIX Security 2024
> There is also a lack of experiments to validate practically the theoretical claims
This is a theoretical paper, and experiments are not necessary to support rigorously proven claims. However, we agree that empirically estimating the privacy guarantees, for example to assess the tightness of our theoretical results, is an interesting idea and we thank the reviewer for this suggestion.
## Questions
> It would be great if the authors could comment on the potential of the approach to generalize to other types of models.
We agree that the generalization of our results to deeper models present significant challenges. However, we believe our findings have the potential to be leveraged in broader settings. For instance, the post-processing theorem ensures that the results also apply to regression problems with activation functions---such as logistic or ReLU regression---provided that Lipschitzness and convexity are preserved.
A promising direction for broader applicability is private fine-tuning of the last layer in deeper neural networks, which maintains the linear regression framework. However, modeling the distribution of the noise in this setting becomes more challenging, as the transformation of the Gaussian input through the layers alters its statistical properties. We leave this for future work.
> About $f$-DP and Rényi DP: "Ideally, it would have been great if the authors could have elaborated on why such notions are necessary compared to the classical DP definition."
We chose to consider $f$-DP because it is a tight way to track the privacy guarantees at all $(\epsilon,\delta(\epsilon))$ budgets as trade-off functions. In fact, $f$-DP is the most informative DP notion for the Blackwell order [2]. While alternatives such as privacy profiles could also be considered, our analysis fundamentally relies on the approximation of trade-off functions. For other privacy definitions, this would require other tools and may lead to looser results. In addition to $f$-DP, we considered Rényi DP for its more interpretable privacy bounds, which are easier to grasp than trade-off functions.
[2] Jinshuo Dong, Aaron Roth, and Weijie J Su. Gaussian differential privacy. Journal of the Royal Statistical Society Series B: Statistical Methodology, 84(1):3–37, 2022. | null | null | null | null | null | null |
Scaling Large Motion Models with Million-Level Human Motions | Accept (poster) | Summary: The paper introduces MotionLib, the first million-level dataset for motion generation, which is 15× larger than previous datasets and includes hierarchical text descriptions. Using MotionLib, the authors train Puppet, a large-scale motion model that demonstrates robust generalization across diverse human activities, including unseen scenarios. To improve motion encoding, they propose Motionbook, which includes:
- A lossless feature representation for motion data.
- A novel 2D lookup-free motion tokenizer that balances fine-grained details and expanded codebook capacity.
Their study emphasizes the importance of scaling both data and model size for advancing motion generation and highlights key insights for achieving generalist motion models. Experimental results show existing models struggle with out-of-domain generalization, whereas MotionLib enables better scalability, positioning it as a benchmark comparable to ImageNet for motion data.
Claims And Evidence: Overall, the explanations are clear and well-structured. They effectively convey the key ideas and provide a solid understanding of the topic.
Methods And Evaluation Criteria: The evaluation criteria sounds reasonable and appropriate for assessing the proposed method.
Theoretical Claims: No theoretical claims in this paper.
Experimental Designs Or Analyses: The experimental design appears sound overall.
Supplementary Material: I reviewed the PDF and videos.
Relation To Broader Scientific Literature: Overall, this work significantly contributes to scaling motion generation and refining motion representation learning. By introducing MotionLib and Motionbook, it bridges the gap between small-scale motion datasets and large-scale generalist models, setting a new benchmark for future research in human motion synthesis and multimodal learning
Essential References Not Discussed: None.
Other Strengths And Weaknesses: ### Strength
- The dataset is significantly larger compared to previous datasets and provides more fine-grained text descriptions. The authors claim that they optimize motion quality using reinforcement learning (RL).
- Experiments validate the effectiveness of scaling and propose a lossless motion representation that is better suited for recovery.
- The 2D encoder indeed enhances performance by preserving more fine-grained information.
### Weakness
- The supplementary material provides too few visualizations, making it difficult to fully assess the richness and quality of the dataset. Some videos are noticeably blurry, which raises concerns about data quality. I also observed that the motion quality is not very high—even after RL optimization, there are still cases of character deformation. It’s unclear whether this is due to perspective issues from Matplotlib rendering or an inherent flaw in the model itself, but either way, it’s a problem that shouldn’t be ignored.
- The claimed motion representation improvement is questionable. From the supplementary videos, foot sliding and pose jittering are still quite prevalent, making it hard to see the claimed benefits. If the proposed motion representation is supposed to enhance stability, where is the concrete proof of its effectiveness? The visual evidence so far doesn’t convincingly support this claim.
Other Comments Or Suggestions: ### Post-Comments of Rebuttal
After discussing with other reviewers, I find that the concerns regarding motion quality still persist. Therefore, I will adjust my score accordingly. That said, I am inclined to lean toward acceptance due to the contribution of the enlarged dataset. I hope the authors will continue refining this dataset post-submission, unlike Motion-X, which saw limited adoption due to its subpar quality.
Questions For Authors: Please see weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer,
Thank you for your thoughtful review and positive feedback. We have carefully considered your questions and suggestions and provide our responses below. Please let us know if you require further clarification.
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## **Response to: Insufficient visualizations in supplementary material, video blurring, motion quality, and deformation issues.**
- **Regarding visualization quantity and video blurring**:
Thank you for your feedback. Due to conference supplementary material size constraints (typically 100MB), we were limited in the number of visual examples we could include and had to compress video resolution. To better demonstrate MotionLib’s richness, we plan to release a dedicated website with additional high-resolution examples upon final publication.
- **Regarding motion quality and deformation**:
We acknowledge that motion data extracted and refined from web videos may still exhibit imperfections (e.g., deformations), even after RL optimization. However, we also feel more positive since our motion model is significantly enhanced using such motion data, demonstrating the scaling law in this task (Table 2, 4). This suggests the larger potential of our MotionLib dataset. As we keep refining this dataset using additional strategies, the gain of performance and generalization could be more significant. Considering this, we consider the building of MotionLib as a long-term iterative process, and our future work can incorporate stricter filtering or advanced algorithms, in addition to current steps we adopted (e.g., 3D keypoint optimization, physics constraints, and RL strategies; see Appendix B.2).
In addition, we suggest the issue of data quality and quantity is a trade-off for large-scale pretraining. Motivated by LLM's pretraining, we believe combining large-scale pre-training with motion fine-tuning on high-quality subsets can further mitigate quality issues while preserving scalability benefits.
## **Response to: Questioning the effectiveness of the claimed motion representation improvement (foot sliding, pose jittering).**
It is important to emphasize that MotionLib’s primary contribution lies in advancing the semantic understanding and generalization capabilities in motion generation, rather than eliminating physical issues (e.g., foot sliding or jittering) entirely. Quantitative improvements in R-Precision, MMDist (Table 3), and OOD generalization (Table 4) demonstrate that our Puppet model achieves superior alignment between text instructions and nuanced human motion, validating the semantic gains we expect. In addition, although MotionLib may include more motion noises compared to datasets like HumanML3D, it excels in the quality and quantity of motion descriptions. After investgation, we notice the texts of HumanML3D, MotionX are hightly duplicate and contain a large amount of noisy texts (e.g.,"moving the hands speaking some thing", "the person's eyeglasses pass"). Instead, our MotionLib avoids these issues by incorporating more clean and diverse texts.
Our methodology follows a "first scale up, then refine down" philosophy.
That means, while physical issues (e.g., foot sliding and jittering) persist in some generated motions —— an expected byproduct of large-scale automated processing — they do not negate the foundational progress of motion semantics. Such trade-offs are inherent to data-driven research at scale. Crucially, MotionLib establishes a robust semantic foundation for general-purpose motion models, enabling future work to address physical fidelity through: (1) further data quality improvements on our MotionLib (e.g., using stricter filtering), (2) post-training refinement (e.g., fine-tuning on high-quality subsets).
We posit that prioritizing scalable semantic understanding is pivotal; physical issues can then be iteratively resolved without compromising the model’s generality.
Thank you again for your valuable feedback. We hope our response clarifies your concerns.
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Rebuttal Comment 1.1:
Comment: Thank the authors for the detailed rebuttal. Most of the concerns have been addressed and I am inclined to accept this paper and hope that MotionLib will contribute to motion modeling research in the future. Therefore I maintain my original scoring as WA.
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Reply to Comment 1.1.1:
Comment: Dear reviewer:
Thank you for your thoughtful review and constructive feedback. We sincerely appreciate your time and effort.
We’re glad our responses addressed most of your concerns. Since you mentioned that the rebuttal resolved most of your concerns and this year’s ratings are limited to 5 levels, we are wondering if you might consider slightly increasing your score to reflect this improvement, or reflecting your positive stance in the final assessment? We believe this would better represent the paper’s improved state.
Of course, we fully respect your judgment. If further clarification would help, we’re happy to provide additional details during the rebuttal period.
Thank you again for your valuable input!
Best regards.
All authors. | Summary: This paper explores various design choices for building large motion models, inspired by the success of LLMs. In the absence of a large-scale motion dataset, it first introduces MotionLib, the first million-level motion dataset, obtained by automatically annotating 3D motion and text descriptions from publicly available videos. It then proposes Pupet, a large motion model trained on the collected MotionLib dataset. Additionally, it introduces Motionbook, a motion encoding method designed to further enhance the model’s representation power. Extensive experiments validate the effectiveness of each design choice and compare the proposed model’s performance with existing motion models.
**Update after rebuttal**
After reviewing the rebuttal and the other reviewers' comments, I will maintain my initial recommendation (weak accept). The authors have addressed most of my concerns, as well as those raised by the other reviewers. However, I *strongly* recommend that the authors revise the manuscript to incorporate the contents of the rebuttal.
Claims And Evidence: The main claims—the effectiveness of the proposed MotionLib, Pupet, and Motionbook—are mostly well-supported by discussions (in comparison to existing baselines) and empirical validation. However, while MotionLib is claimed to be the first million-scale motion dataset, the below paper (published at ECCV 2024) also introduces a motion dataset with 100 million frames for training a large motion model:
[1] Zhang *et al.*, Large Motion Model for Unified Multi-Modal Motion Generation, ECCV 2024.
Is the "million-scale" referred in this paper based on the number of sequences or frames? Clarifying this aspect would help distinguish MotionLib from existing datasets.
Methods And Evaluation Criteria: Both the proposed method and evaluation criteria are mostly reasonable. I especially appreciate how this paper considers diverse training datasets, evaluation datasets, and baseline models to demonstrate the effects of core design choices in building a large motion model.
However, it seems that one highly relevant work was excluded as a baseline in the experiments:
[1] Zhang *et al.*, Large Motion Model for Unified Multi-Modal Motion Generation, ECCV 2024.
Theoretical Claims: There is no theoretical claim that requires formal proof in this paper.
Experimental Designs Or Analyses: I verified the validity of all experimental designs in the main paper and found no issues with the existing designs. However, I notice a lack of **qualitative** comparisons with existing baselines (e.g., MotionGPT, T2M-GPT), despite the paper providing comprehensive quantitative comparisons.
Supplementary Material: I reviewed the assets provided as supplementary material. One concern is that I noticed some samples in the dataset exhibit significant foot sliding. Although it is mentioned that these samples were assigned "smaller weight during pretraining" (lines 200–201), I wonder whether it would be more effective to completely discard samples with severe foot sliding instead.
Relation To Broader Scientific Literature: This paper presents a comprehensive analysis of the core design choices (e.g., training dataset scale, data encoding method) in building large motion models. Its technical contributions are closely related to those in the literature on other large model training (primarily LLMs), although the problem domain is different, and some contributions (e.g., motion representation) are specific to the motion generation problem.
Essential References Not Discussed: As mentioned several times in the above comments, I believe this paper is highly relevant to this work, as it claims similar contributions (e.g., large-scale dataset collection, large motion model training). Discussing this paper would be necessary to better distinguish the unique contributions of this paper.
[1] Zhang *et al.*, Large Motion Model for Unified Multi-Modal Motion Generation, ECCV 2024.
Other Strengths And Weaknesses: **Strengths.**
I appreciate how this paper provides comprehensive experimental results on key design choices for building large motion models, offering valuable insights for future research in this area. Additionally, the collected large-scale motion dataset and the pre-trained large motion model have the potential to be highly beneficial to the research community.
**Weaknesses.**
Comparisons with an important related work [Zhang *et al.*, ECCV 2024] are missing. Without discussing this work, it is difficult to fully assess the unique contributions of this paper. Additionally, while the paper provides extensive quantitative comparisons, including *qualitative* comparisons with existing baselines would be also important.
Other Comments Or Suggestions: * Please clarify whether "million-scale" in this paper refers to the number of sequences or frames. If it does refer to the number of sequences as mentioned in the paper, it would be helpful to also provide the total number of frames in the collected dataset for additional clarity.
* Typo in line 30: "an compact" should be corrected to "a compact."
Questions For Authors: Please refer to the above comments. Was there a specific reason why [Zhang *et al.*, ECCV 2024] was not discussed in the paper?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer,
Thank you for your thoughtful review and positive feedback. Below are our responses to your questions and suggestions. Please let us know if you require further clarification.
## **Response to: the discussion of LMM [1] and Dataset Comparison**
We appreciate you highlighting the relevant work of LMM [1]. Below, we clarify the scale and unique contributions of MotionLib in comparison:
- **Dataset Scale**: The term "million-scale" in our paper refers to the number of motion sequences. MotionLib contains 1.2 million (1.2M) motion sequences (as in Table 1), totaling 137 million (137M) frames. In contrast, LMM’s dataset comprises 320K sequences and 100M frames. Thus, MotionLib is currently the largest motion generation dataset in both sequence count and total frames. We will explicitly add the frame count to Table 1 for clarity.
- **Key Distributions**:
- **Task Focus**: MotionLib is optimized for text-to-motion generation, featuring 2.48M fine-grained text-motion pairs (including fine-grained part-level descriptions). LMM, meanwhile, targets multi-modal inputs (text/image/audio).
- **Performance**: On HumanML3D, Puppet outperforms LMM in R@1, R@3, and MMDist, showing better text-motion alignment. Notice that our FID performs worse than LMM. We attribute this to the difference of used motion tokenizer. As shown in Table.7, our 2D-LFQ simply performs competitive to vanilla VQ, but showing large improvement as the data become larger and diverse. This means that our lookup-free tokenizer has more advantage when facing large-scale scenarios and thus requires more training data. It's also important to note that Puppet exhibits a strong agent capability to follow the user's instructions empowered by the LLM. Among existing LLM-based generalist models, Puppet excels these models in performance.
||R@1|R@3|MMDist|FID|
|-|-|-|-|-|
|LMM|0.525|0.811|2.943|0.04|
|Puppet-LFQ|0.528|0.82|2.875|0.141|
We will expand the discussion of LMM in the revision, emphasizing MotionLib’s scale, annotation richness, and task-specific advantages.
[1] Large Motion Model for Unified Multi-Modal Motion Generation. ECCV 2024
## **Response to: Qualitative Comparisons with MotionGPT & T2M-GPT (Experimental Designs)**
Thank you for this useful feedback! We agree qualitative examples are important. We will add qualitative comparisons of motion results generated by our Puppet versus T2M-GPT and MotionGPT for the same text prompts in the subsequent revision.
## **Response to: The Foot Sliding Issue in Dataset (Supplementary Material)**
Thank you for raising the issue of foot sliding. Indeed, automatically estimating motion data from large-scale web videos inevitably introduces noises, including physical implausibilities like foot sliding.
The most important reason we choose to down-weight these low-quality samples rather than completely discarding them is: we adopt two-stage training to address the impact of noisy data:
- **Motion pretraining — Information Preservation:** In a million-scale dataset, even noisy samples might contain valuable motion patterns or contextual information. Discarding them completely could lead to the loss of potentially useful information.
- **Motion instruction Tuning — Future Optimization:** More importantly, after obtaining a good base model through large-scale motion pre-training. High-quality subsets can later refine the model via instruction tuning, further improving generation quality and physical realism.
Such approach is motivated by the great success of LLMs. In the pretraining stage of LLM, a large amount of corpus is quite dirty. However LLM can still gain massive knowledge from it and develop good responsive ability through instruction-tuning.
In addition, we have other considerations to incorporate these part of data:
- **Maximizing the Scale Utilization:** Our goal is to explore the potential of large-scale data training. Retaining all samples (even if down-weighted) maximizes the utilization of diversity brought by the data scale.
- **Down-weight is a Common Strategy:** When dealing with large noisy datasets, reducing the weight of noisy samples via the loss function is a mature and effective strategy that allows leveraging data scale while mitigating the negative impact of noise.
As a summary, we believe that pursuing an increase in data scale first, followed by continuous improvement of data quality via further refinement and filtering, to enhance model performance through down-weighting and subsequent fine-tuning, is an effective pathway for developing large motion models at this stage.
## **Response to Other Comments (e.g., adding total frame count and correcting typo)**
Thank you for pointing them out.
- We will explicitly add the total frame count of MotionLib (approx. 137 million frames) in the revised Table 1 or relevant text.
- We will correct "an compact" to "a compact" in line 30 in the revised version.
Hoping our response clarifies your concerns.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for providing a thoughtful rebuttal. Most of my existing concerns are clearly addressed, except for the qualitative comparisons, which cannot be reported during the rebuttal phase. I strongly encourage the authors to include such results in the revision later.
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Reply to Comment 1.1.1:
Comment: Dear reviewer,
Thank you for the time and effort you have dedicated to evaluating our work.
We are pleased that our responses have addressed most of your issues. Since you mentioned that the rebuttal resolved your concerns, and given that ICML only has 5-level rating this year, we are wondering if you might consider slightly adjusting your score, or reflecting your positive stance in the final assessment to better represent the improvements after rebuttal?
That said, we fully respect your judgment and expertise. If any further clarification would be helpful, we would be happy to provide additional details during the rebuttal period.
Best,
All authors | Summary: This paper proposes a dataset, a VQVAE, and a motion generation model. The dataset MotionLib comprises over 1.2M motion sequences with hierarchical and detailed text annotations. The VQVAE uses a 2D-LFQ for a lookup-free tokenizer. The text-to-motion model is trained on the proposed dataset and VQVAE.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes, the videos.
Relation To Broader Scientific Literature: Related to human motion generation.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
- The text annotations are detailed on body parts.
- Using a simulated environment to eliminate some physical issues like jittering and foot-sliding is reasonable.
Weaknesses:
- For the dataset, the accuracy of WHAM is limited. I have tried WHAM and other motion estimation methods, but none of them produce decent results which are valid to serve as the ground truth. As shown in Figure 2, the estimated motion is not accurate.
- Many details about the data refinement are not clear. For example, how is the RL performed, which is the simulated environment, how to find and mark slipping with smaller weight.
- For the VQVAE, 2D motion quantization is already well-used in motion generation, e.g., ParCo, MogenTS.
- For the text-to-motion model, it uses a well-used autoregressive model for motion generation, without new designs.
- In the experiments, the compared methods miss many recent methods with better performance, e.g., MoMask, MoGenTS, LaMP, Diversemotion, ReMoDiffuse, Stablemodiffusion, Fg-T2M++.
- For the out-of-distribution experiments, the FID is large, which illustrates that the generalization is still weak. Also, I suggest evaluating on HumanML3D while only training on different scales of MotionLib. This should demonstrate the value of MotionLib.
- For table 2, the training and evaluation setting is not clear. It states it utilizes the autoencoder retrained on motion-x and motionlib, but also states the training sets are HumanML3D only, Motion-X only, MotionLib-0.5, MotionLib-full. Also, it writes "retrain", then how is the pretrain performed?
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Dear Reviewer,
We appreciate your valuable feedback. Due to space constraints, **we only provide concise responses below but would present more during discussion.** Please let us know if any clarification is needed.
## W1: WHAM accuracy & dataset validity
While no motion estimation algorithm is perfect, our data pipeline (3D keypoint optimization, physics constraints, RL tuning — App B.2) refines initial estimates. Despite noises, Table 2 & 4 show large-scale motion pretraining improves generalization by exposing models to diverse motions. MotionLib provides a foundational resource especially high-quality texts. Its quality can be improved via future algorithm updates and filtering. Scale is critical given current data scarcity.
## W2: Data refinement details (RL, simulation, slipping handling)
We refine motion sequences using the PHC policy (Luo et al., 2023) in IsaacGym, which achieves high tracking accuracy (97.1% on AMASS, 95.7% on Human3.6M). The process involves:
- Inputting video-extracted motion to PHC for physics-compliant tracking (balancing, reducing jitter/sliding).
- Using PHC to generate physically plausible motions in IsaacGym, with termination conditions (e.g., early termination for balance loss) flagging low-quality sequences.
- Downweighting flagged sequences during Puppet model training—a common practice for handling noisy data—to prioritize high-quality samples.
## W3: 2D motion quantization is already used
While ParCo and MoGenTS explored 2D motion quantization, the core innovation of our MotionBook (including 2D-LFQ) lies in its lookup-free (LFQ) mechanism and **its application in the context of large-scale training**. Unlike traditional VQ (limited to small codebooks, e.g., 512/1024 codes), LFQ avoids codebook collapse and supports 16K+ codes, enabling scalable learning on our million-scale MotionLib dataset. This addresses a key bottleneck in prior works, which were not designed for such diversity and scale.
## W4: T2M model uses a standard AR architecture, lacking novel design
While Puppet uses a standard LLM architecture, our key contribution is the first Scaling Law study for motion generation, systematically analyzing data/model size impacts—similar to foundational VLM work like LLaVA, which also relied on standard architectures.
In text-to-motion, we argue that constructing large-scale motion data with rich, hierarchical text descriptions (MotionLib) and designing effective motion encodings (MotionBook) to bridge text-motion alignment are themselves significant contributions. Our endeavour in data construction and labeling aims to establish a foundation for future large motion models.
## W5: Missing comparisons with some recent methods
Thank you for highlighting these recent works. For a more comprehensive comparison, we include their publicly reported results on HumanML3D. Some methods (e.g., LaMP, MoGenTS) were concurrent or very recent (within 4 months) and were not initially compared.
Notably, current T2M methods include specialist models optimized on specific datasets and LLM-based generalist models (aiming for broader instruction/task generalization via LLMs), like our Puppet. Puppet excels among generalist models (Table 3) and remains highly competitive on R@1, R@3, and MMDist compared to specialist models.
||R@1|R@3| MMDist|FID|
|-|-|-|-|-|
|Momask|0.521|0.807|2.958|0.045|
|ReMoDiffuse|0.51|0.795|2.974|0.103|
|Puppet|0.528|0.82|2.875|0.141|
## W6: High FID in OOD experiments; suggestion to evaluate on HumanML3D (HM3D) using MotionLib
Higher OOD FID Explanation: The UNSEEN-90K test set comprises 11 subsets with substantial distribution shifts from training data, including synthetic data, activity-specific datasets, and varied capture environments. The elevated FID in this challenging OOD setup is expected, similar to observations in other motion tasks (e.g., music-to-motion in LMM). More importantly, Table 4 validates that large-scale training with diverse, large-scale MotionLib data (vs. HM3D or MotionX alone) significantly boosts OOD performance.
HM3D Evaluation: Thanks for the suggestion. We remove all HM3D data from MotionLib and trained models on varying scales of remaining data (0.6M–1.2M samples), then evaluate on the HM3D test set. Results are shown below:
|Train Data Size|R@1|R@3|MMDist|FID|
|-|-|-|-|-|
|0.6M|0.176|0.369|2.980|9.408|
|1.2M|0.208|0.441|2.964|7.983|
## W7: Lack of clarity for train/eval settings in Table 2 ("retrain", "pretrain").
These terms are distinct in our context:
- Retrain: Refers to training the evaluation model (motion autoencoder) separately for each benchmark (MotionX and MotionLib), following HM3D paper’s architecture. This ensures metric fairness (FID, R-Precision) across datasets.
- Pretrain: Describes Puppet’s training:
- Initialize with public LLM weights (GPT-2, LLaMA).
- Extend vocabulary with motion tokens.
- Continue pretraining on target datasets (HumanML3D/MotionX/MotionLib subsets) via autoregressive loss.
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Rebuttal Comment 1.1:
Comment: Thank the authors for the rebuttal. Some of my concerns have been addressed, but some remain:
- My biggest concern is the accuracy of the ground truth, which has not been addressed. As admitted by the authors and presented in Figure 2, the accuracy of poses estimated from videos is not valid to serve as the ground-truth. I agree that no video motion estimation algorithm is perfect, therefore we should explore other ways to obtain more accurate poses, e.g., RGB-D video estimation, multi-view estimation, or MoCap system. I know these ways are more expensive to build a large-scale dataset, but that's the way building a dataset should be. Using the estimation from videos is too cheap to build a dataset. It has been proved that the inaccurate poses are useless: In Motion-X, only the MoCap part helps the learning while the video estimation part works not well. I agree that "Scale is critical" but scale without accuracy is useless. Improving the scale with inaccurate video estimation is somewhat easy.
- According to the table in Rebuttal W6, the model trained on the proposed dataset performs badly on HumanML3D dataset, indicating a lack of generalization. This demonstrates that the proposed dataset does not help.
- For the method, as admitted by the authors, there is no much novelty and the core contribution is the application in the context of large-scale training. According to the experiments and the rebuttal, the performance of the proposed method is worse than other methods. So the novelty and the performance of the method are both not strong. Of course I agree that a good large-scale motion dataset would be itself a significant contribution and enough for acceptance. But the paper continues emphasizing the method, making me confused about which is the core of the paper, the dataset or the method? After clarification by the authors, I believe the dataset is the core, in which case I should be strict with the dataset.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer,
We're inspired that our reply addresses some of your questions! Thank you for engaging with our rebuttal. We greatly appreciate this opportunity to further clarify our approach:
**Q1: Dataset Accuracy**
A: We understand the concerns regarding video estimation accuracy, but MotionLib's value lies in: 1) large-scale video (motion) estimation, 2) multi-step refinement, and 3) high-quality text annotation. We believe considering all three aspects provides a comprehensive view of its contribution.
Our core points are:
1. **Motion Refinement Pipeline:** Our refinement pipeline (3D optimization, physics simulation, RL tuning) significantly mitigates initial noise and enhances data usability (e.g., successful RL tracking yields high-quality balanced motion), a key advantage over MotionX.
2. **High-Quality Text:** 2.48M hierarchical, high-quality text annotations are a core contribution driving language-conditioned modeling. This distinguishes it from prior datasets where text quality was often overlooked. E.g., (1) HumanML3D has redundancy (≥6 identical descriptions for each each text); (2) MotionX has data leakage (≥15% of test descriptions appear in training) and grammatical issues. MotionLib's text quality is higher. This contribution should not be ignored, especially for text-to-motion.
3. **Scale and Precision Balance:** The motion generation field suffers from severe data scarcity. We believe prioritizing a million-scale dataset with "video estimation + refinement + high-quality text" provides a crucial starting point and resource for the community, more beneficial than waiting for "perfectly accurate data". Future iterations can improve quality upon this base, serving as an iteratively optimizable repository. This aligns with large model pre-training history (e.g., early datasets like HowTo100M weren't flawless but catalyzed development). Regarding MotionX, its scale and annotation richness are incomparable to MotionLib, making direct comparison potentially inappropriate.
**Q2: OOD Performance on HumanML3D (HM3D)**
A: We argue that the zero-shot cross-dataset results in W6 should not directly lead to the conclusion that the "dataset is useless". Reasons are:
1. **Domain Gap:** Data in MotionLib (post-HM3D removal) – mainly web videos/other datasets – has significant distribution differences from HM3D (mainly AMASS MoCap). Direct zero-shot cross-domain evaluation is inherently challenging; performance drop is expected. This reflects domain adaptation difficulty, not dataset ineffectiveness.
2. **Value of Pre-training:** Large-scale pre-training's core value is providing a strong generalization foundation and understanding of broad concepts. Pre-trained models are typically easier to adapt to new domains via fine-tuning on a small amount of target-domain data. As shown in Table 5, performance improves with subsequent instruction tuning on high-quality data, proving the value of large-scale pre-training.
3. **Performance Improvement:** Even in the zero-shot setting, the R@1 improvement (0.176 to 0.208) and FID decrease (9.4 to 7.98) directly indicate that larger-scale MotionLib data does enhance the model's generalization capability.
**Q3: Method Novelty, Performance, and Core Contribution**
A:
1. **Novelty:** We disagree that our method entirely lacks novelty. We introduce clear innovation in Motion Encoding, namely MotionBook. 2D-LFQ, with its lookup-free mechanism and ability to scale codebook capacity for large-scale data, is a novel solution addressing bottlenecks in existing VQ methods for massive motion datasets – an area unexplored by prior methods.
2. **Performance:** Our method, as a generalist LLM model, achieves SoTA results compared to other generalists and is competitive with specialist models on standard T2M metrics. We did not cite some works (e.g., LAMP, Fg-T2M++) as they were unpublished or lacked code at the time. We are willing to discuss them in revision. However, per ICML concurrent work policy, this should not be grounds for rejection. Furthermore, our LLM-based model handles diverse scenarios/tasks effectively. In contrast, specialist models lack broad semantic knowledge.
3. **Contributions:** (1) Large-scale Dataset MotionLib: Unprecedented scale and annotation richness. (2) MotionBook: An innovative encoding method for large-scale training. (3) Scaling Law Study: First systematic study of scale effects, validating the LLM framework's potential.
We believe the dataset and the method are complementary, together forming the core contribution of this work. The large-scale dataset MotionLib provides a crucial foundation for validating the effectiveness of MotionBook and studying Scaling Laws. Conversely, efficient encoding methods and an understanding of Scaling Laws are also essential for effectively utilizing the MotionLib data.
Thank you again for your valuable time and feedback. We hope this clarification better conveys the value and contribution of our work. | Summary: The paper investigates scaling motion generation models based on million-level data and LLM-style architecture. The authors first contributes a million-level human motion dataset, named MotionLib. Training models on this data, they highlight the importance of scaling both data and model size for advancing motion generation. To better integrate the motion modality, they propose MotionBook for fine-grained motion features and efficient motion tokenizer. The empirical findings from this work offer valuable insights to researchers in the field.
Claims And Evidence: yes, all claims are well supported
Methods And Evaluation Criteria: yes, they compare their method with other LLM-based methods. The evaluation data comprising both public and self-collected data. They follow the conventional evaluation criteria.
Theoretical Claims: N/A
Experimental Designs Or Analyses: yes, I check the experiments.
The experiments design primarily follows the experiments design of LLM (scaling data/model, architecture design, etc.). Additional, they provide experiments to validate the effectiveness of the proposed motion book.
One question is about OOD experiment. in Table 4, the authors are suggested to explain the UNSEEN-90K dataset. How the evaluation data differs from training data? (different motion categories? synthetic v.s. realistic? different complexity?) It is suggested to provide some representative examples.
Supplementary Material: Yes, I read the appendix, and the html.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths: The authors provide extensive experiments and this works could be a solid work if the dataset and code are released in future. The intuition of Motionbook makes sense.
Weakness: The design of Motionbook treats motion sequence as 2D image, and I suppose the authors use convolution layers to extract features? Comparing with RNN/Transformer, convolution network maybe cannot perform well in global feature extraction. How do the authors handle this?
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer,
Thank you for your thoughtful review and positive feedback. We have carefully considered your questions and suggestions and provide our responses below. Please let us know if you require further clarification.
---
## **Response to: Questions about UNSEEN-90K Dataset in OOD Experiments**
In our OOD experiments (Table 4), the UNSEEN-90K testing set is constructed by excluding 11 subsets (~90K samples) from the full MotionLib dataset. The remaining data (primarily Motion-X and web-derived data) serves as the training set.
The excluded subsets are intentionally diverse to ensure significant distributional shifts from the training data, enabling a robust evaluation of OOD generalization. These subsets include:
- Synthetic data: gta_human [1], bedlam [2] (distinct from web-derived training data captured in the real world).
- Domain-specific activities: FIT3d [4] (fitness), RICH [5], ARCTIC [11] (human-object interactions), EgoBody [7] (social interactions).
- Diverse environments: PoseTrack [3], MPI-INF-3DHP [6] (in-the-wild settings), Human36M [8], CHI3d [9], KIT [10] (daily activities captured in the lab).
This selection strategy demonstrates that the UNSEEN-90K testing set exhibits substantial distributional shifts compared to our training data, allowing us to rigorously assess the model’s OOD generalization. As shown in Table 4 in our main paper, models trained on MotionLib outperform those trained solely on HumanML3D or Motion-X, highlighting the benefit of large-scale, web-sourced motion data.
Regarding the examples. Thank you for this constructive suggestion. We will incorporate additional visualization examples in the appendix in our revised manuscript.
[1] Playing for 3D Human Recovery. TPAMI 2024
[2] BEDLAM: A Synthetic Dataset of Bodies Exhibiting Detailed Lifelike Animated Motion. CVPR 2023
[3] PoseTrack: A Benchmark for Human Pose Estimation and Tracking. CVPR 2018
[4] AIFit: Automatic 3D Human-Interpretable Feedback Models for Fitness Training. CVPR 2021
[5] Capturing and Inferring Dense Full-Body Human-Scene Contact. CVPR 2022
[6] Monocular 3D Human Pose Estimation In The Wild Using Improved CNN Supervision. 3DV 2017
[7] EgoBody: Human Body Shape and Motion of Interacting People from Head-Mounted Devices. ECCV 2022
[8] Human3.6m: Large scale datasets and predictive methods for 3D human sensing in natural environments. TPAMI 2013
[9] Reconstructing Three-Dimensional Models of Interacting Humans. CVPR 2020
[10] The KIT Motion-Language Dataset. Big data 2016
[11] ARCTIC: A Dataset for Dexterous Bimanual Hand-Object Manipulation. CVPR 2023
---
## **Response to: The Limitation of MotionBook’s Global Feature Extraction**
Thank you for your question. You raised a valid concern regarding MotionBook’s use of 2D convolutions for motion encoding. We clarify our design choices below:
**1. Division of Roles**
- **Motion Tokenizer**, which focuses on quantizing continuous, high-dimensional motion features into discrete, low-dimensional token sequences, effectively capturing local spatio-temporal features and achieving a compact representation. 2D convolutions are well-suited for this due to their computational efficiency and inductive bias for local patterns.
- **LLM backbones**, which handles global feature modeling and long-range dependencies within the input token sequence via Transformer self-attention, addressing the limitation of CNNs for global context reasoning.
This hybrid design combines the strengths of CNNs (local feature extraction) and Transformers (global modeling), ensuring efficient and effective motion encoding.
**2. Why CNN Over Alternatives (e.g., RNN or Transformers)?**
- **Fair Comparison**: Most prior motion tokenizers (e.g., VQ, RVQ) use CNNs, therefore we maintain consistency for fair benchmarking.
- **Empirical Findings**: We experimented with Transformers but observed no performance gain, likely due to the limited data amount and lower resolution compared to vision tasks where ViTs excel.
We appreciate your insightful feedback and hope our responses address your concerns. Thank you again for your time and constructive comments! | null | null | null | null | null | null |
Locality Preserving Markovian Transition for Instance Retrieval | Accept (poster) | Summary: This paper tackles the problem of instance retrieval, or finding the image most similar in a dataset to a query image. Existing methods suffer from long-range propagation of similarity information, which the authors improve on with three components. BCD- They improve similarity propagation by combining multiple adjacency graphs rather than relying on a single all-to-all graph. LSE- transforms distances between pairs into probability distribution between a set of k nearest elements. TMT- they define a new cost metric as the transition cost between 2 elements, which is the term they minimize. They show impressive results across a range of datasets and against a large number of baselines.
Claims And Evidence: Yes, the authors provide extensive and impressive quantitative results against existing works.
Methods And Evaluation Criteria: Yes, the authors provide a comprehensive list of benchmarks and evaluate their proposed method on a set of datasets.
Theoretical Claims: The methods proposed in this paper are well established in other areas. They borrow ideas from graph theory, probabilistic methods, and optimal transport. When applied to this setting, they all seem fitting.
Experimental Designs Or Analyses: I am unfamiliar with the current state of the art in instance retrieval, but it all looked reasonable.
Supplementary Material: No supplementary materials were provided.
Relation To Broader Scientific Literature: While they apply their idea to instance retrieval, I would be very curious to see if their idea can be applied to the attention operation in transformers. A transformer's similarity matrix might be sensitive to exact similarity values between pairs, but a more informed similarity could improve performance. This would increase computational complexity but, depending on the application, could be a worthwhile tradeoff. This could hypothetically be interesting follow-up work.
Essential References Not Discussed: The works they include in the paper seem reasonable and comprehensive.
Other Strengths And Weaknesses: This is only a slight weakness, but the task of instance retrieval has limits as far as applicability to real-world scenarios. I can see this work being an interesting basis for future work.
Other Comments Or Suggestions: This paper is very well laid out and easy to follow.
Questions For Authors: I am impressed with the paper presented. I have no recommendations for rebuttal.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your positive assessment and recognition of our contribution to manifold reranking. In this work, we address the fundamental challenge of manifold ranking by introducing the proposed **Locality Preserving Markovian Transition (LPMT)**. Our approach establishes a structured, long-term transition process that effectively connects distinct distributions within the graph, ensuring reliable information propagation at each step. To mitigate the impact of unreliable connections, BCD adaptively ensembles diffusion processes across multi-level graphs to generate a robust similarity matrix. This is achieved through a joint optimization framework that refines both the combination weights and the diffusion objective, which we solve efficiently using a fixed-point iterative approach. Subsequently, LSE embeds each instance as a probability distribution within the manifold space, and LPMT bridges distant distributions through a sequence of locally constrained transitions. This design not only preserves the intrinsic manifold structure but also maintains essential local characteristics, with the minimal transition cost serving as a principled metric for enhanced retrieval performance.
Building on this foundation, **migrating the manifold ranking algorithm to Transformers presents an intriguing research direction.** As the core of the Transformer architecture, the self-attention mechanism models pairwise token relationships via dot-product similarity between query and key vectors. While stacking Transformer layers facilitates deeper integration of information, it does not inherently capture the underlying manifold structure of token embeddings within each layer. Given the extensive adoption of Transformers, incorporating manifold ranking, despite its additional computational cost, could improve the reliability of similarity estimation. Since our current algorithm is designed for complex manifold spaces and deep learning-based retrieval tasks, further simplifications are necessary to enhance its robustness for broader applications. We will further investigate these aspects in the future.
Regarding **practical deployment**, while our primary focus is on improving manifold ranking effectiveness, several optimizations can enhance efficiency. For computationally intensive operations such as diffusion, an **offline strategy** can be employed to precompute and store results in a database, allowing the LSE distribution of each instance to be maintained in advance. Upon receiving a new query, its probability distribution can be efficiently estimated via linear aggregation of neighboring samples, significantly reducing online computation. Likewise, the exact computation of TMT cost can also be approximated to improve efficiency. By decoupling complex operations into **offline preprocessing and efficient online retrieval**, we can partition the main workload accordingly, making real-world deployment more practical. We will continue investigating these optimizations in future work.
In conclusion, he proposed LPMT framework serves as a strong foundation for effective manifold ranking, demonstrating high performance across multiple retrieval benchmarks. Future work will focus on integrating it with Transformer architectures and optimizing efficiency for practical deployment. | Summary: The paper introduces the Locality Preserving Markovian Transition (LPMT) framework to improve instance retrieval by overcoming the limitations of traditional diffusion-based re-ranking methods. Standard methods suffer from diminishing positive signals over long diffusion paths, which weakens their discriminative power. LPMT addresses this by combining Bidirectional Collaborative Diffusion to build robust similarity matrices, Locality State Embedding to encode instances as probability distributions for enhanced local consistency, and a Thermodynamic Markovian Transition process that bridges distant instances via local intermediate states. This integrated approach effectively preserves local relationships while ensuring accurate global retrieval, leading to notable improvements in performance on benchmark datasets.
Claims And Evidence: The paper claims a novel image retrieval strategy based on extracted image features. It constructs an improved similarity matrix using Collaborative Diffusion (BCD), which automatically integrates diffusion processes on multi-level affinity graphs. To enhance global discriminative power without sacrificing local effectiveness, the authors introduce the Locality State Embedding (LSE) strategy, representing each instance as a locally consistent distribution within the underlying manifold. Finally, Thermodynamic Markovian Transition (TMT) is proposed to perform a constrained time evolution process within local regions at each stage. The definition and formulation is easy to follow.
Methods And Evaluation Criteria: Yes, the paper conducts large-scale evaluations on standard datasets, such as Oxford5k (ROxf) and Paris6k, using the standard retrieval metric (mAP), and further divided into Easy, Medium and Hard categories. I have concerns regarding the setting where an extra collection of one million distractor images is incorporated to form the large-scale ROxf+1M and RPar+1M datasets. Will this operation introduce an inductive bias toward positive results?
Theoretical Claims: Lemma A.1 to Lemma A.5 are well-known results in matrix analysis, how does they relate to Section A.2? Would the assumption of "each
transition only takes place in local regions" be too strong to be generalized? I would like the authors and other reviewers to double check proof B.2, especially B.21 and B.24 which are not convincing to me.
Experimental Designs Or Analyses: Please check evaluation part comment.
Supplementary Material: Please check theoretical part comment.
Relation To Broader Scientific Literature: No
Essential References Not Discussed: No
Other Strengths And Weaknesses: This method is based on extracted features by off-the-shell models, which could be a limitation for downstream methods though sound theoretical framework has been proposed in this paper. Robustness of this method to weaker features or ablations might be a strong proof of the effectiveness of this framework.
Other Comments Or Suggestions: I would like the author to add a pipeline figure to visualize the pipeline in future versions.
Questions For Authors: 1. I have concerns regarding the setting where an extra collection of one million distractor images is incorporated to form the large-scale ROxf+1M and RPar+1M datasets. Will this operation introduce an inductive bias toward positive results?
2. I also have concerns about the time cost associated with building the initial similarity diffusion, as well as whether additional computational optimization is required for incoming data. This could potentially affect the practical application value of this work.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1: Will the incorporation of extra distractor images introduce an inductive bias?**
An additional one million distractor images are introduced to simulate a large-scale image database. Compared to the original ROxf and RPar datasets, the expanded database includes a larger number of hard negative samples for each query, significantly increasing retrieval difficulty (ROxf-M baseline drops from 67.3 to 49.5). When applying reranking methods, these distractors introduce noise into the manifold structure, disrupting information propagation and posing a greater challenge to the algorithm.
**Q2: The role of Lemma A.1 and A.5 in the proof.**
We explicitly present Lemma A.1 and A.5 because they are essential to establish the convexity of the objective function and the convergence of the iterative formulation. In Section A.2, when constraining $\beta$ and updating $F$, we reformulate the objective function as Eq. (A.8) using properties of the Kronecker product. The convexity proof hinges on demonstrating that the Hessian matrix is positive-definite, which is a nontrivial step that requires Lemma A.1 to derive the nature the matrix $S$. Lemma A.5 is instrumental in proving the convergence of the iterative process in Eq. (A.14) and establishing its equivalence to the closed-form solution. Specifically, in Eq. (A.16), the second summation follows the structure of a Neumann series, necessitating the result of Lemma A.5.
While these steps may be derivable for experts in matrix analysis, we include these lemmas to ensure a rigorous and self-contained exposition.
**Q3: Question about the assumption of local transition.**
Limiting each transition to a local region aims to mitigate information loss over multiple iterations in the diffusion process, ensuring reliability at every step. Experiments on various feature databases have demonstrated its effectiveness. We believe that maintaining local characteristics in complex manifold spaces contributes to better overall performance.
**Q4: Explanation of proof B.2.**
We clarify Proof B.2 by summarizing its main idea and then explaining the derivation of Eqs. (B.21) and (B.24).
(1) The core idea is to prove Eq. (B.16) by establishing both directions: RHS ≤ LHS and LHS ≤ RHS. For RHS ≤ LHS, we show that the transition cost of any flow $T_t$ is no less than the Wasserstein distance (We bridge this by introducing a Riemann sum, which is also in the form of a transportation cost). For LHS ≤ RHS, we aim to construct a flow $T_t$ whose cost matches that of a given transport plan $Q$. Note that many such flows may exist; we only need to show existence.
(2) To prove LHS ≤ RHS, we construct $T_t$ through the following steps:
$Q$ → $(q _ m)$ (B.20) → $q_t$ (B.21) → $T_t$ (B.22–25). In (B.21), we construct a flow $q_t$ with constant velocity for each vertex-to-vertex transport. That’s why we use a linear time parameter $t$ at the vertices $r_m$ and $s_m$, while keeping the other vertices fixed. Eq. (B.24) follows directly from substituting the first and second equations in (B.23) into the third. By replacing $\dot{q}_t$ on the left-hand side with the expression in (B.22), and substituting $T_t[r_m, r_m]$ with $-T_t[s_m, r_m]$, we obtain that $T_t$ satisfies (B.24).
We emphasize again that **we only need to prove the existence** of a valid $T_t$ via construction, uniqueness is not required.
**Q5: Robustness of the proposed method.**
To verify the robustness of our algorithm across different feature databases, we employ not only the classic R-GeM for feature extraction but also more advanced models such as DOLG/CVNet and weaker models like MAC/R-MAC. This enables evaluation across both stronger and weaker features, with our method consistently outperforming these benchmarks (see Appendix C). Additionally, our algorithm also demonstrates reliability in text-image retrieval tasks, as discussed in our response to reviewer ij2o.
**Q6: Time cost and computational optimizations.**
Thank you for raising this important concern. While our primary focus is on improving the effectiveness of manifold ranking, we have some feasible optimizations to address the essential problem of practical deployment.
The BCD component incorporates a diffusion process that operates with a time complexity of $O(n^3)$. Empirically, for a graph with 5000 nodes, executing 12 iterations requires approximately 0.3s. To enhance computational efficiency, we can adopt an offline strategy to precompute high-complexity operations within the database, wherein each image is encoded with a diffusion-based similarity in advance. Upon receiving a query, its diffusion-based similarity can be approximated by linearly aggregating neighboring samples. Similarly, the TMT distance can be precomputed within the graph, enabling reranking with efficiency comparable to kNN. While approximation introduces some performance overhead, we will continue exploring the trade-off between accuracy and efficiency. | Summary: Existing re-ranking methods tend to reduce discriminative power over several steps. This paper proposes the LPMT framework for accurate manifold distance measurement, thereby enhancing the retrieval process. The proposed method is supported by several theoretical analyses, and experiments demonstrate significant performance improvements over baseline methods.
Claims And Evidence: The proposed research problem lacks clear articulation and would benefit from more precise formulation. The writing throughout the manuscript requires improvement to enhance readability and comprehension. Regarding empirical validation, the experimental section needs strengthening with more rigorous evaluation protocols and comprehensive analysis of results.
Methods And Evaluation Criteria: The proposed methods appear to address the stated problem effectively. However, the evaluation criteria require further explanation, as several metrics are not clearly defined or justified in the current presentation.
Theoretical Claims: The theoretical claims presented in the paper appear sound; however, the work would benefit significantly from more thorough comparison with existing literature.
Experimental Designs Or Analyses: Yes. The experimental design appears comprehensive and provides reasonable support for the work’s central claims.
Supplementary Material: yes, all
Relation To Broader Scientific Literature: Retrieval technology has emerged as a critical advancement across various domains. Consequently, this work on retrieval methods has potential applications spanning multiple scientific areas, underscoring its broader impact beyond the immediate field of study.
Essential References Not Discussed: The discussion on retrieval methods for textual data requires further expansion.
[1] Su, H., Yen, H., Xia, M., Shi, W ., Muennighoff, N., Wang, H. Y., ... & Yu, T. (2024). Bright: A realistic and challenging benchmark for reasoning-intensive retrieval. arXiv preprint arXiv:2407.12883.
[2] Chen, J., Lin, H., Han, X., & Sun, L. (2024, March). Benchmarking large language models in retrieval-augmented generation. In Proceedings of the AAAI Conference on Artificial Intelligence (Vol. 38, No. 16, pp. 17754-17762).
Other Strengths And Weaknesses: Strengths：
1. The research problem addressed in this paper is significant, as retrieval technology represents an important area of investigation across multiple fields.
2. The experimental results demonstrate performance improvements over the selected baseline methods.
Weakness：
1. The stated claim could be made clearer. For instance, the authors note that instance retrieval focuses on identifying images visually similar to a given query image at a large scale. However, retrieval methods have already been widely used in Large Language Model (LLM) contexts, such as Retrieval-Augmented Generation (RAG). Therefore, it would be beneficial to clarify why the work specifically focuses on image-only retrieval, and whether or how lessons from broader retrieval applications (e.g., text-based retrieval) might be incorporated or contrasted.
2. The motivation for focusing on image retrieval should be more compelling. Highlighting the unique challenges of image retrieval—such as differences from natural language processing (NLP) retrieval tasks—would emphasize the distinctiveness and importance of this work.
3. The datasets used in the experiments appear to be outdated. Recent benchmarks have been introduced for retrieval tasks, including:
[1] Su, H., Yen, H., Xia, M., Shi, W ., Muennighoff, N., Wang, H. Y., ... & Yu, T. (2024). Bright: A realistic and challenging benchmark for reasoning-intensive retrieval. arXiv preprint arXiv:2407.12883.
[2] Chen, J., Lin, H., Han, X., & Sun, L. (2024, March). Benchmarking large language models in retrieval-augmented generation. In Proceedings of the AAAI Conference on Artificial Intelligence (Vol. 38, No. 16, pp. 17754-17762).
Including or comparing against these newer benchmarks could strengthen the evaluation and demonstrate the method’s relevance to current retrieval challenges.
4. The discussion of retrieval-related research is not sufficiently comprehensive, especially regarding developments in the NLP domain. Incorporating relevant NLP-focused retrieval studies and explaining how they align or differ from this work would offer a clearer picture of the broader retrieval landscape.
Other Comments Or Suggestions: It likewise appears to be a weakness.
Questions For Authors: It likewise appears to be a weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate your valuable comments on the advanced applications of retrieval in the NLP domain. However, we believe that the key focus of retrieval tasks differs between the fields of image and NLP. We hope the following response will be helpful to emphasize our contribution to manifold ranking and explain why our experiments focus on image retrieval.
**Q1: Motivation for focusing on image retrieval and its challenges.**
Our proposed method addresses a fundamental problem in manifold ranking, which aims to **utilize the inherent structure of the data space** to improve retrieval performance (as discussed in Section 1, 3). Specifically, manifold ranking assumes that instances within a dataset exhibit intrinsic similarities, and when embedded into a semantic feature space, **similar instances tend to form a low-dimensional manifold**. Unlike the conventional approach that relies solely on pairwise similarity between the query and individual samples, manifold ranking **capitalizes on the latent relationships among instances within the database** to improve retrieval performance.
In image retrieval, each image is represented by a global feature, forming a vector database for retrieval. Refining initial search results by re-extracting image features with a more powerful model is often **computationally expensive and impractical**. Therefore, an efficient strategy is required to enhance retrieval performance by **leveraging the structural relationships among existing feature representations, rather than relying on additional feature extraction.** This characteristic aligns well with the principles of manifold ranking, such that existing algorithms predominantly use it as their primary evaluation benchmark.
Conversely, modern NLP tasks tend to go beyond measuring retrieval effectiveness solely based on textual semantic similarity. For instance, recent benchmarks like "Bright" place greater emphasis on **logical reasoning and deep text comprehension**. These tasks require finer-grained semantic alignment and reasoning ability between words in the query and documents, **which differs from our task setting that relies solely on original global semantic features.** To enhance the quality of retrieval results, current NLP-driven re-ranking methods primarily leverage more advanced models, such as LLMs and Cross Encoders, to **conduct a deeper analysis of the interactions between queries and documents at the token level.** Given that our method is focused on exploring the semantic relationships among candidates based on global features, it is not well-suited for NLP retrieval tasks that necessitate a fine-grained linguistic understanding.
Nevertheless, our approach still remains effective for textual retrieval tasks focused on content search, including text-image retrieval and specific dense model-based information retrieval applications.
**Q2: Broader applications.**
Regarding the concern in Weakness 1 about the applicability of our method to broader retrieval tasks, while it is primarily designed for image retrieval, it is also effective for various textual retrieval tasks with a semantically dense feature database. Leveraging VLMs and pretrained dense retrieval models to process the image and corpus databases, our method can be applied to text-image retrieval and information retrieval tasks. As shown in Tab. 1, 2, our method effectively improves retrieval performance, particularly in text-image retrieval tasks.
Tab 1. Zero-shot text-image retrieval on Flickr30k, based on CLIP and BLIP.
||R@1|R@5|R@10|
|:-: |:-:|:-:|:-:|
|CLIP|55.7|80.8|88.3|
|CLIP+Ours|66.7|93.6|96.8|
|BLIP| 68.3 |89.4|94.2|
|BLIP+Ours|70.4|95.5|98.4|
Tab 2. Information retrieval on ArguAna, based on the pretrained model from BEIR.
||nDCG@1|nDCG@5|nDCG@10|
|:-:|:-:|:-:|:-:|
|Baseline|20.6|37.5|42.6|
|Ours|27.3|47.0|52.2|
**Q3: Evaluation and datasets.**
ROxf and RPar are among the most widely used datasets in image retrieval, with the hard protocol posing significant challenges. Nearly all retrieval models report their performance on these benchmarks to ensure fair comparisons, and prior reranking studies consistently use R-GeM as a baseline. Additionally, since different retrieval models yield varying levels of feature representations, it is beneficial to assess the generalizability of LPMT.
Evaluating our method on NLP and RAG benchmarks such as Bright and RGB falls beyond the scope of this study. Our approach applies graph theory to model feature databases, ensuring more reliable results by exploiting the underlying manifold information. We believe these benchmarks are more suited for evaluating LLMs and NLP-based rerankers.
**Q4: Literature review.**
We appreciate the recommendation to further discuss NLP-focused studies, which could enhance the overall understanding of the retrieval landscape. We will further discuss their distinctions in the revised version.
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Rebuttal Comment 1.1:
Comment: thanks for rebuttal and i have updated my score
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Reply to Comment 1.1.1:
Comment: Thanks for your valuable feedback and positive reassessment. We sincerely appreciate your support! Your suggestions will be instrumental in further refining our manuscript. | Summary: In this paper, the authors focused on the diffusion-based re-ranking for instance retrieval. Considering the issue of decaying positive signals and the impact of disconnections in the existing methods, the authors proposed the Locality Preserving Markovian Transition (LPMT) framework. The proposed method consists of three key modules, including BCD, LSE, and TMT. Specifically, BCD integrates diffusion processes across separate graphs to establish strong similarity relationships. LSE encodes each instance into a distribution to enhance local consistency, and TMT connects these distributions through a thermodynamic Markovian transition process for efficient global retrieval while maintaining local effectiveness. Extensive experiments prove the effectiveness of the proposed method.
Claims And Evidence: The authors present a comprehensive set of experiments on multiple datasets with different difficulty levels and using various deep retrieval models. For example, in Table 1, LPMT shows significant improvements in mAP compared to other methods such as AQE, αQE, and CAS under the medium and hard evaluation protocols on ROxf and RPar datasets. The ablation studies also provide evidence for the effectiveness of each component of LPMT.
Methods And Evaluation Criteria: The proposed methods make sense for the problem of instance retrieval. The use of diffusion-based processes in BCD is a well-established approach in the field, and the innovation of integrating multiple graphs through bidirectional collaborative diffusion helps to capture the manifold structure more effectively. LSE's encoding of instances into distributions and TMT's use of a thermodynamic transition process are novel and address the limitations of traditional diffusion-based methods.
Theoretical Claims: The theoretical claims in the paper seem to be well-founded. The authors provide a detailed mathematical derivation for each component of LPMT. It would be beneficial if the authors could provide more intuitive explanations for some of the theoretical concepts, especially for readers who are not familiar with the complex mathematical theories of stochastic thermodynamics.
Experimental Designs Or Analyses: The experimental designs are sound. The authors compare LPMT with a wide range of re-ranking methods, including query expansion methods, diffusion-based methods, context-based methods, and learning-based methods.
Supplementary Material: I reviewed the supplementary material. The supplementary material provides additional experimental results based on different deep retrieval models (MAC, R-MAC, DELG, SENet), which further validates the effectiveness of LPMT. However, the supplementary material could be more organized, and some of the figures could be better labeled for easier interpretation.
Relation To Broader Scientific Literature: The key contributions of the paper may add a new perspective to the field of instance retrieval.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strong points:
The paper has a solid theoretical foundation, with detailed mathematical derivations and proofs for the proposed methods.
Weak points:
The proposed method is relatively complex, with multiple components and hyperparameters. This may limit its practical application in some scenarios where computational resources are limited.
Other Comments Or Suggestions: Given the complexity of the method, it would be beneficial if the authors could explore ways to simplify it without sacrificing performance. This could make the method more accessible for practical applications.
Questions For Authors: 1. In the BCD component, the optimization process involves iteratively updating the similarity matrix F and weights β. How to ensure the stability of this iterative process?
2. In the TMT component, the use of the Wasserstein distance as an approximation for the minimum transition flow cost is based on certain assumptions. How sensitive is the performance of LPMT to these assumptions?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1: Concerns about the involvement of multiple components and hyperparameters.**
Regarding the concern about multiple components and hyperparameters. Although our method consists of multiple modules, each can be implemented in a relatively straightforward manner. For example, the BCD objective can be iteratively solved following Algorithm 1, while TMT reduces to solving an optimization problem (Eq. 20) for the optimal transition strategy. These processes require simple inputs (e.g., BCD only needs the adjacency matrix $W$), ensuring low coupling and easy deployment. Ablation studies demonstrate the robustness of LPMT, showing that most hyperparameters have minimal impact on performance. When adapting to new tasks, only a few key parameters ($k_1$, $k_2$, $\theta$) need adjustment, reducing the tuning effort when adapting to new tasks. Additionally, high-complexity steps can be decoupled and precomputed (see Q2), further improving efficiency in resource-limited scenarios.
**Q2: Simplify the implementation for practical applications.**
Thanks for the concern about the accessibility to practical applications. While our primary focus in this work is to improve the effectiveness of manifold ranking, there are some feasible optimizations to simplify the implementation or enhance efficiency.
Firstly, BCD module can be replaced with Gaussian kernel function to approximate the manifold-aware similarity when computation resource is limited. Additionally, we can adopt an offline strategy to precompute high complexity operations within the database, such that each image can be embed with the diffusion-based similarity in advance. When a new query arrives, we can approximate its diffusion-based similarity with other instances by linearly aggregating neighboring samples. Similarly, the TMT distance can also be precomputed within the graph, allowing us to perform online reranking with an efficiency close to kNN. We will continue to investigate methods to simplify the deployment of the reranking system without sacrificing performance.
**Q3: How to ensure the convergence when jointly optimize $\beta$ and $F$ in BCD.**
The convergence of the optimization is ensured by the following factors:
(1) When $\beta$ is fixed, the objective function (denoted as $J(\beta, F) = \lambda\|\beta\|_2^2/2 + \sum\beta _ {v}H^{v}$) is convex with respect to $F$ and admits a unique minimum point. Similarly, when $F$ is fixed, the function is convex with respect to $\beta$ and also has a unique minimum.
(2) In our optimization, we construct a sequence of $\beta^{(k)}$ and $F^{(k)}$ using the following update rules:
$$
\beta^{(k)} = \arg\min\limits_{\beta} J(\beta, F^{(k)}),$$
$$
F^{(k+1)} = \arg\min\limits_{F} J(\beta^{(k)}, F).$$
The resulting variable sequence is $\{(\beta^{(0)}, F^{(0)}), ..., (\beta^{(k)}, F^{(k)}), (\beta^{(k)}, F^{(k+1)}), (\beta^{(k+1)}, F^{(k+1)}), ...\}$. The corresponding sequence of objective values $J$ is non-increasing.
(3) If $J(\beta^{(k)}, F^{(k)}) = J(\beta^{(k)}, F^{(k+1)})$, then by the uniqueness of the optimal point discussed in (1), we have $F^{(k)} = F^{(k+1)}$, and subsequent updates of $F$ and $\beta$ will remain unchanged. The same holds if $J(\beta^{(k)}, F^{(k+1)}) = J(\beta^{(k+1)}, F^{(k+1)})$.
(4) If the condition in (3) never occurs, then the sequence of objective values strictly decreases at each iteration. Since $J \geq 0$, the sequence converges to a finite value $J^*$.
**Q4: Assumptions for TMT component and their influence to the performance.**
In our proposed TMT component, we assume that each transition is governed by a master equation and occurs within a local region. As demonstrated in Appendix B, we prove that the transition cost between two neighboring distributions is equivalent to the Wasserstein distance, where the distance on the graph serves as the cost matrix. This locality assumption mitigates information loss over multiple iterations of the diffusion process and effectively models long-term transitions between distributions in the graph. Compared to directly computing the flow cost between distant distributions, our approach ensures the reliability of each transition while reducing the computational complexity over the entire graph, thereby improving both performance and efficiency.
**Q5: Suggestions for providing more intuitive explanations and improving the organization of supplementary materials and image labels.**
Thank you very much for the valuable feedback. We appreciate your suggestions and will incorporate more intuitive explanations of the theoretical concepts to enhance clarity. In the revised version, we will also reorganize the image captions and supplementary materials for better readability and coherence.
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Rebuttal Comment 1.1:
Comment: Thanks for your detailed response. I have updated the score.
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Reply to Comment 1.1.1:
Comment: Thanks very much for your kind and constructive feedback. We sincerely appreciate the time and effort you dedicated to reviewing our paper. We will carefully revise the manuscript based on your suggestions. | null | null | null | null | null | null |
Learning Latent Graph Structures and their Uncertainty | Accept (poster) | Summary: Exploiting the structure of the problem of interest is often key to achieve good generalization with the trained model. For real world applications, it might be known that underlying relational information is shaping the observed data but this latent structure remains often hidden. Some previous works have proposed algorithms learning jointly the topology of the data and the model that leverage it to make predictions in the observational space. Over existing approaches do not quantify how close is the learned latent structure to the true one.
The authors of this submission propose to fill this gap and consider the latent topology as a random object. They provide an algorithm to jointly learn the distribution of the graph latent structure and the one of the observations that relies on it. Their algorithm is supported by a theoretical result showing that minimizing the population loss lead to a well calibrated latent distribution and optimal point prediction.
Claims And Evidence: The theoretical results is validated on a synthetic dataset. The numerical results support the theoretical claims but I think some aspects could be improved:
- I do not totally agree with the authors when they explain that for reall applications, we don't have access to the true distribution of the topology. I think the authors might have considered a case the graph is known and fixed (i.e. the distribution of the latent structure is a Dirac mass) and they could have used their algorithm assuming that the graph is not observed. As the number of observations increased, we expect the learned distribution of the latent graph to converge to this Dirac mass.
- The authors prove Proposition 4.1 by giving a concrete example where calibration is not achieved by minimizing the point-prediction loss. However, this example is very specific and it would have been interesting to run the standard methods (optimizing the point prediction loss) on their synthetic dataset to see if the learned distribution of the latent structure is calibrated or not. This is important since the main contribution claimed by the authors is to propose a way to learn calibrated latent distribution. Therefore it would have been valuable to show that existing methods do not lead to good calibration in most cases.
Methods And Evaluation Criteria: Please see my comments in section "Claims And Evidence".
Theoretical Claims: I checked the correctness of the proofs of the theoretical claims.
Experimental Designs Or Analyses: Please see my comments in section "Claims And Evidence".
Supplementary Material: I reviewed the supplementary material. I appreciate the effort made by the authors to discuss additional numerical results and to provide more insight on their theoretical results.
Relation To Broader Scientific Literature: The paper relates to the literature on Graph Structure Learning, and more generally to the problem of identifiability in the statistical literature.
Essential References Not Discussed: I am not expert in the field and thus other reviewers will have much more relevant comments for this section.
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: Here are a few typos:
- Theorem 5.2 contains some typos.
- In Eq.(10), a probability distribution is missing under the last expectation.
- Before section 6.1: "additional specifics are detailed"
- In Section A.3 of the appendix, a $\phi$ is missing when refering to $P^{\theta,\phi}_{y\mid x}$ at several locations. In the same section at line 664, I think $\psi$ should not have a superscript $*$.
- At line 732, R^N should be \mathbb R^N.
- At line 736: "therfore"
Questions For Authors: Let me first thank the authors for their work. I really appreciate the effort made to investigate quite deeply both the theoretical (such as in section A.4) and practical (such as section B with the variance reduction method) aspects of their approach.
- Regarding Section A.4, the injectivity hypothesis is discussed for a graph neural network. The analysis shows the assumption is satisfies under mild condition for a very simple GNN. Could you comment on the injectivity assumption for more realistic GNN ? My intuition tells me that the injectivity will be less likely to hold for bigger/deeper network.
- The synthetic dataset considered relies on a probabilistic model to generate graphs which looks a bit adhoc. It would be interesting to consider a more structure and realistic model where probability of connection between two nodes is given by k(x_i,x_j) for some kernel k where x_i and x_j are observed features associated to nodes i and j.
Ethical Review Concerns: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Claims and Evidence**
**a**.
First of all, we appreciate your constructive comments. We see your point, but the issue with the proposed approach is not that the graph structure provided in the real-world dataset is not a distribution - we agree that the ground-truth distribution can be a Dirac distribution.
The problem is that there are no guarantees that the provided graph structure is, or is close to, the underlying graph distribution that generated the data; many times the graph structure provided with the data is built using some heuristics (e.g., node similarity or physical distance between sensors).
This is one of the reasons why Graph Structure Learning emerged as a field.
The synthetic dataset - and, ultimately, our theoretical results - serves to overcome this limitation. Nonetheless, we perform the following additional experiment.
**a (additional experiment)**.
To demonstrate that our method is able to learn sensible graph distributions in real-world settings, we train a neural network on air quality data in Beijing (Zheng, et al. 2013). The neural network consists of a GRU unit to process each time series, followed by a GNN with a learnable graph structure. At the following [link](https://anonymous.4open.science/r/learning_latent_graph_structures_and_their_uncertainty/README.md) we share the graph structure learned by the model with the lowest validation loss. As you can see, our approach learns a reasonable graph.
**b**.
We agree with you, and indeed we ran that experiment in Section 6.3. Note that the first five rows in Table 2 consider either point-prediction losses or losses from the existing literature.
As shown, the calibration performance is worse than the proposed method.
**Other Comments Or Suggestions**
Thank you for spotting those typos, we have fixed all of them.
**Question For Authors**
**1**.
At the moment, we have only partial results for generic multi-layer GNNs.
On the one hand, Corollary A.1 in Appendix A provides a meaningful insight for continuous GNNs: it states that even if a multi-layer GNN fails to be injective for most inputs, injectivity at a single point $\bar x$ is sufficient for our results to apply.
On the other hand, following the proof of Proposition A.2, if $P_x^*$ is absolutely continuous, then $f(\cdot, A)$ is injective almost surely.
While we do not have a proof to offer yet, the two comments above are encouraging that a proof might be found.
**2**.
We considered the multivariate Bernoulli distribution because it is general enough to model all graph distributions over independent edges; moreover, it is widely used in the Graph Structure Learning literature (e.g., Francheschi et al. 2019, Elinas et al. 2020, Sun et al. 2021, Cini et al. 2023).
We agree that considering other distributions, including input-dependent ones, is relevant. Considering the set of experiments already carried out (7 in the paper and 2 during the rebuttal) and that they already rigorously validate our claims, we leave this extension as future work. Finally we stress that the theoretical results apply to more general distributions. Thank you for your relevant comments.
**References**
- Zheng et al. "U-air: When urban air quality inference meets big data.", 2013.
- Franceschi et al. "Learning discrete structures for graph neural networks.", 2019.
- Elinas et al. "Variational inference for graph convolutional networks in the absence of graph data and adversarial settings.", 2020.
- Sun et al. "Graph structure learning with variational information bottleneck.", 2021.
- Cini et al. "Sparse graph learning from spatiotemporal time series.", 2023. | Summary: In this paper, the authors investigate the calibration of latent graph structure distributions in the context of graph structure learning. They propose an optimization procedure for a predictive probability model that ensures not only learning the best predictive model but also calibrating the latent distribution of the underlying graph structure. To compute the gradient of the Maximum Mean Discrepancy (MMD) loss, the authors rely on Monte Carlo (MC) sampling and reduce the variance introduced by MC through a control variates approach. Experimental results demonstrate the effectiveness of the proposed method.
Claims And Evidence: The claims are generally well-supported by theoretical analysis and experimental results.
Methods And Evaluation Criteria: The proposed method is reasonable.
Theoretical Claims: The theoretical claims are clearly presented.
Experimental Designs Or Analyses: The experimental design and analysis are generally sound. Some concerns can be referred to the below 'Weakness'.
Supplementary Material: I read the part of the appendix, such as the proof section.
Relation To Broader Scientific Literature: NAN
Essential References Not Discussed: NAN
Other Strengths And Weaknesses: • Strengths:
Overall, I think the problem of calibrating the latent graph structure distribution to be important. The proposed method is grounded in theory and is well organized, and the sampling-based learning approach appears practical. The empirical results are also interesting.
• Weaknesses:
a. In Equation (1), y is typically considered a discrete graph label, whereas in Equation (2), \hat{y} (the model output) is usually continuous. The predictive distributions of discrete y and continuous \hat{y} cannot theoretically be the same, so is Assumption 5.1 satisfiable?
b. The injectivity condition in Theorem 5.2 seems rather strong. For instance, in some graph classification tasks, different subgraph structures A may correspond to the same graph label y.
c. The designed method does not appear to leverage the unique characteristics of graph data. Moreover, all experiments are conducted on synthetic datasets, which raises concerns about the real-world applicability of this method.
d. When generating synthetic datasets, assuming each edge is generated independently is overly simplistic. Why not employ more commonly used graph generation models?
e. The authors do not compare the performance of their method against existing graph structure learning methods.
Other Comments Or Suggestions: NAN
Questions For Authors: What exactly is x in Equation (1)? Can it be understood as the node feature matrix of the input graph?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Wa**.
There might be some misunderstanding here, please allow us to clarify that the assumption is indeed satisfiable.
Both Equations 1 and 2 can model continuous or discrete outputs, but their respective outputs $y$ and $\hat y$ take values from the *same* set $\mathcal Y$.
$\Delta$ is a dissimilarity measure between distributions over the same set $\mathcal Y$ for both its arguments (i.e., $P_1,P_2$).
Assumption 5.1 relates to $\Delta$, and it is known to be satisfied, e.g., by $f$-divergences and some integral probability metrics
**Wb**.
Please note that our Theorem 4.2 demands only injectivity over a set of inputs with non-zero probability; in the case of Corollary A.1, this reduces to ensuring injectivity at a single point $\bar x$. The assumption relates to the data-generating process and the associated learning problem.
The particular case of graph classification is relevant due to the discrete nature of $\mathcal Y$. Here, ensuring calibration of the latent variable presents increased complexity, regardless of the chosen loss function.
According to our results, distributional losses should still be favored over point-prediction losses even in this setting, if calibration of the latent variable is among the goals.
**Wc**.
Please note that Proposition A.2 and Lemma A.3 specifically relate to graph neural networks and we empirically demonstrated that all the developed results are applicable in Graph Structure Learning scenarios.
Secondly, as commented in the paper, ground-truth knowledge about the latent graph distribution is not available in any real-world datasets we are aware of. Our paper addresses this lack of information in two ways: (i) we derived theoretical guarantees to reduce the need for empirical assessments and (ii) we rigorously validated and tested our approach on synthetic data that provides the required ground truth.
Nonetheless, to provide evidence of the effectiveness of our method in real-world scenarios, we perform an additional experiment. Please see our response "**a (additional experiment)**" to Reviewer qZGr.
**Wd**.
Parameterizing the graph structure as a set of Bernoulli distributions allows us to cover *any* distribution over graphs of independent edges. Moreover, this is a common parameterization in the graph structure learning literature (Francheschi et al. 2019, Elinas et al. 2020, Sun et al. 2021, Cini et al. 2023), other than being easier to inspect and visualize. Testing other distributions is indeed possible.
Furthermore, we stress that the theoretical results are not restricted to Bernoulli distributions.
**We**.
Please note that we do provide a comparison with existing literature (see Section 6.3 and Table 2). However, as our paper discusses loss functions, we compared the proposed approach with loss functions used in the literature.
**Question**
Yes, $x$ can be understood as the node feature matrix provided as input to the prediction model. It can contain discrete and continuous attributes, as common in GSL setups, but also time series, as in spatiotemporal data analysis.
**References**
- Franceschi et al. "Learning discrete structures for graph neural networks.", ICML 2019
- Elinas et al. "Variational inference for graph convolutional networks in the absence of graph data and adversarial settings.", NeurIPS 2020
- Sun et al. "Graph structure learning with variational information bottleneck.", AAAI 2021
- Cini et al. "Sparse graph learning from spatiotemporal time series.", JMLR 2023
---
Rebuttal Comment 1.1:
Comment: Thank you for the author's response. Most of my questions are addressed.
I will keep my score leaning towards acceptance. | Summary: This paper carefully studies the problem of how the optimal latent graph can be learned given observational information from both theoretical and empirical perspectives. It proves that optimizing the usual point prediction does not guarantee calibration of the adjacency matrix distribution. It also provides a loss function that guarantees simultaneous calibration of the latent variable and optimal point predictions. A sampling-based strategy with variance reduction is designed to tractably compute the loss functions. Experimental results on carefully designed synthetic datasets verify the theoretical claims, and also demonstrate the advantages when theoretical assumptions are not fully satisfied.
**Update after rebuttal**
I have read the response from the authors. Since my original recommendation was to accept, I will maintain my recommendation.
Claims And Evidence: The claims are well supported by both theoretical and empirical results.
Methods And Evaluation Criteria: 1. The proposed method is theoretically motivated.
2. Sampling-based estimation of MMD and the control variate for variance reduction are properly derived.
3. The computational complexity is analyzed and it seems acceptable for practice.
4. The method is evaluated comprehensively in experiments. See **Experimental Designs Or Analyses** for detailed comments.
Theoretical Claims: The theoretical claims on the limitation of point prediction and the optimality of the proposed loss functions are supported by rigorously stated theorems with proofs.
Experimental Designs Or Analyses: The experimental design is rather comprehensive.
1. The experiments are conducted on synthetic datasets because the ground truth graphs are known and it is easy to manipulate the generation process to create different settings. This is reasonable, because I prefer to consider this paper a theory paper and the experiments are for the proof of concepts.
2. The experimental settings are clearly described and well justified.
3. Under the normal setting, the results show that the MMD loss is suitable for joint learning. The variance reduction component is effective. The method is applicable for large-scale graphs. All these results provide strong support for the theoretical analysis in the main text.
4. Considering that the theoretical analysis relies on Assumption 3.1 which ensures optimal solution, this paper conducts a series of experiments to see what will happen when the assumption is violated. The results show that the proposed method is still effective under different settings.
5. The MMD loss is compared with classical choices of loss functions in GSL. The results show that MMD is advantageous in predicting the target variable and superior in recovering the latent graphs.
Supplementary Material: I have read the appendices.
Relation To Broader Scientific Literature: This paper is related to graph structure learning (GSL), latent graph inference, and distribution calibraction.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
S1. This paper explains a long-troubling issue in GSL in theory under some simplified assumptions.
S2. The notations are used accurately, theoretical results are clearly stated and the proofs are concise to read.
Weaknesses:
W1. Figure 2-11 appear in the appendix but are mentioned in the main text. Please consider better organizing the presentation of the experimental results to make the main text more self-contained.
Other Comments Or Suggestions: C1. Even though Assumption 3.1 ensures the existence of optimal parameters, it can be hard to reach in practice. For example, when inferring latent graphs from multivariate time series, prediction error is inevitable, and there could be more than one best graph. The authors can discuss such limitations when applying their theory to real-world applications.
References:
A Graph Dynamics Prior for Relational Inference. In AAAI, 2024.
C2. In Appendix A.2, to argue that minimizing $\mathcal{L}^{point}$ does not guarantee calibration, a counter-example is created based on a specific choice of the loss function, i.e., the MAE. However, in the statement of Proposition 4.1, the authors seem to claim that the conclusion always holds for all choices of $\ell$. Can you make the statement of Proposition 4.1 more precise or provide any proof or thoughts to support that counter-examples can always be constructed?
C3. In Assumption 5.1, can we relax the statement of "$\triangle(P_1,P_2)=0$ if and only if $P_1=P_2$" to "$\triangle(P_1,P_2)=0$ if and only if $P_1=P_2$ almost surely"?
C4. In Appendix B, why is it reasonable to approximate the numerator of Eq. (10) with $\mathbb{E}[L(A)]\mathbb{E}[(\nabla_\theta\log P^\theta(A))^2]$? When will the approximation be accurate?
C5. In Line 687 of the proof of Corollary A.1, should we write $A\not=A'$ to ensure that $\bar{\epsilon}>0$? Besides, since $\delta$ is chosen for $f^*(\cdot,A)$, how can we ensure that $\lVert f^*(\bar{x},A')-f^*(x,A')\rVert<\epsilon$? That is, why does the second inequality in Line 695 hold? I don't fully understand the proof. Can you provide more explanation?
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **W1**.
We appreciate your suggestion. If the paper is accepted, we will use part of the camera-ready additional page to improve the presentation.
**C1**.
Yes, this is a relevant point. This is why we run experiments in controlled settings to test our method beyond those assumptions. In particular, Section 6.1 studies the joint learning problem and shows that the processing function can be approximated well.
Section 6.2 ("Perturbed $f_{\psi^*}$") tests cases of unsuccessful training, showing that even if the GNN makes prediction errors, the graph structure can be learned with good quality. Section 6.2 ("Generic GNN as $f_{\psi}$") considers a family of GNNs that does not fulfill Assumption 3.1. Also in this setting we were able to learn meaningful distributions.
Finally, we would like to highlight that point-prediction functions simply fail to calibrate the graph structure even when the GNN is fixed to the true (supposed to be known) processing function.
**C2**.
Thank you for pointing out this potential source of misunderstanding. Proposition 4.1 states that calibration is not granted for a generic point-prediction loss, not that for any choice it will necessarily fail. In Appendix A.2, we showed that optimizing a commonly adopted metric, the MAE, can be problematic in that context; other specific metrics are not directly investigated in this paper.
We will revise the paper to prevent any possible confusion.
**C3**.
Thank you for your relevant question. For the purpose of Theorem 5.2, Assumption 5.1 can be relaxed to hold almost surely with respect to $P_x^*$ - as you suggested. However, we think the current statement of Assumption 5.1 is easier to grasp.
**C4**.
Thank you for carefully reading the appendices.
The more the two terms in the expectation are independent the more the approximation is accurate.
The main reason to accept this approximation is that it enables an easy estimation of the optimal $\beta$.
**C5**.
Yes, we are considering $A \not = A'$ in that line. We fixed the typo, thank you.
Regarding the second question, for every $A$ we can find a $\delta_A$ granting $||f^*(\bar{x}, A) - f^*(x, A)||<\epsilon$; this follows from the continuity of $x\mapsto f^*(x, A)$. As we have finitely many $A$, we take $\delta=\min_{A\in\mathcal A} \delta_A$. Thank you for raising the point, we will clarify it.
---
Rebuttal Comment 1.1:
Comment: Thank you for resolving all of my concerns. Please revise the paper accordingly. I will keep my overall recommendation. | Summary: This paper deals with the problem of learning on graph in a setting where the graph (Adj. matrix: A) is unobserved and is to be estimated from the training data (node features: x, node labels/targets: y). It theoretically shows that the optimal point estimate does not guarantee the calibration of the latent graph structure's distribution. However, if a certain type of loss between the ground truth and model's prediction distribution is zero, then that both achieves the optimal point estimate of the targets and recovers the true distribution of the graph structure under restrictive assumptions. A variance reduction strategy using control variates is adapted for the specific setting. Numerical experiments on small scale graphs are conducted to verify the theory presented.
Overall, the theoretical contribution of this work is inadequate and the empirical validation is rather weak (detailed comments/questions/suggestions in later sections).
**Update:** The authors' rebuttal helped in partially addressing some of my concerns, particularly the comparison with one existing baseline on a synthetic dataset shows that the proposed method can generate graphs with similar statistics. However, I still think that **a)** the novel theoretical contribution (the proofs are extremely simple, MMD is an existing loss function, and control variate is another widespread technique for variance reduction) is limited primarily due to unrealistic and restrictive modelling assumptions, **b)** the experiments seriously lack investigation of performance and comparison with existing techniques with various parameterizations of the graph generative models. I am raising my score to 2 to acknowledge the authors' effort during the rebuttal.
Claims And Evidence: 1) Optimal point estimate of the targets does not lead to calibration of graph distribution: Proposition 4.1 shows that.
2) MMD minimization between the pushforward measures of targets leads to optimal point estimate of the targets and calibration of distribution of A: Theorem 5.2 shows that. (I have some questions about the usefulness of this, which are asked in 'questions to authors' section below)
Methods And Evaluation Criteria: Results in Table 2 verifies the theory presented numerically.
Theoretical Claims: Please see "Claims And Evidence" section above.
Experimental Designs Or Analyses: The experiments numerically verify the theory presented (my questions are written below)
Supplementary Material: I have checked the proofs, they are correct to the best of my knowledge.
Relation To Broader Scientific Literature: While the results are correct, their impact in advancing the field of learning on graphs is minimal in my view, because of impractical and restrictive modelling assumptions and lack of real-data experiments (check the weakness section for detailed comments and questions).
The discussion of related work is confusing and inaccurate at places (check the weakness section for details).
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1) The paper is moderately well written and easy to read.
Weaknesses:
1) Relevance to GNN community: The main theoretical results presented in this paper are only marginally relevant to advancing knowledge in the area of learning on graphs. Specifically, the theoretical results are valid for any latent variable model which can be characterized by eq 1. The stated assumptions are not specific to graph domain in any discernable way as well. It is not clear how the results of this paper can be helpful for any GNN researcher or practitioner in any way.
2) Restrictive modelling assumptions: The model in eq. 1 is rather limited. First, this idea that $y= f(x, A)$ is a deterministic function of $x$ and $A$ limits its applicability to classification problems, where the label is a K-ary variable, sampled from $p(y|x, A)$. Similarly, if the targets are noisy in a regression setting, then a deterministic mapping is inadequate.
3) Impractical modelling assumptions: The model in eq. 1 considers $x$ observed and factorize the joint distribution as follows:
$p(y, A|x) = p(A) \times Indicator_fun(y=f(A, x))$. In other words, eq. 1 does not consider any dependency between A and x. But, this is typically not the case in real world graph datasets and for problems of practical interest. For example, Kalofolias 2016 (https://arxiv.org/pdf/1601.02513) considers learning a graph from smooth signals. Intuitively, if the node features are similar for a node pair $(i,j)$, then $A_{i,j}$ should be higher and vice versa, this type of approach models the dependency between $x$ and $A$ explicitly. Even for the datasets, used extensively for evaluation of GNNs, there is dependency between the graph structure and node features. For example, on homophilic graphs (e.g. Cora, having stochastic block model structure approximately), the node feature similarity is heavily correlated with graph connectivity. It is not clear whether the results in this work can address such setting.
4) Other assumptions: How does the injectivity assumption work for any GNN with more than one layers? Otherwise, theorem 5.2 is of little practical significance.
5) Other comments about theoretical results: The 'proof' of Proposition 4.1 only requires the understanding that two distributions can differ even if a certain moment matches. Given the trivial nature of this results, the choice of stating it as a formal proposition is questionable.
Moreover, the algorithm does not guarantee that we can obtain $\phi^*$, so how the requirement of knowledge of the 'true' GNN in Theorem 5.2 is justified?
5) While the authors argue in favor of not including any real data experiments and existing baselines, it is not at all convincing. For example, if the 'true' distribution that generates the graph is unknown, one could still run the proposed method with some chosen parameterization (to capture some useful inductive bias) to perform an estimation of $P(A)$, and then use the learned model for sampling graphs and then check whether graph statistics match with the 'true' distribution. This avenue gives an indirect route to assess calibration. Bayesian GNNs (Zhang et al., 2019) and Variational GNN (Elinas et al., 2020) could serve as baselines with minimal modifications in that setting.
6) Discussion of related work is far from being accurate. For example, the authors write "Some approaches from
the literature model the latent graph structure as stochastic (Kipf et al., 2018; Franceschi et al., 2019; Elinas et al.,
2020; Shang et al., 2021; Cini et al., 2023), mainly as a
way to enforce sparsity of the adjacency matrix." Kipf et al., 2018 propose GCN on a fixed graph, they do NOT 'model the latent graph structure as stochastic '.
Other Comments Or Suggestions: N/A
Questions For Authors: Please address the issues raised in the previous sections.
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **W1**.
Part of our results can indeed be applied to more general latent variable models, and we view this broader applicability as a strength rather than a weakness. As shown in the Experiments Section, our theoretical results can be successfully applied to Graph Structure Learning problems, making them relevant to the GNN community. Furthermore, some results are specific to GNNs (e.g., Proposition A.2).
**W2 W3, W4 and W5**.
Our paper highlights the critical role of the loss function to effectively achieve calibration; this specific formulation and set of assumptions serve this goal.
Some assumptions can be relaxed, broadening the applicability of our findings. However, we believe that our developments lay a solid foundation enabling further developments.
We expect - and have validated with different experiments (refer to Sections 6.1 and 6.2) - that the theory remains valid beyond certain assumptions.
In the following points, we provide additional evidence to support that our results can be generalized to address your concerns further:
- **W2)**
We performed an additional experiment where $p(y|x,A)$ is a continuous distribution both in the system model (Eq. 1) and the approximating model (Eq. 2). Specifically, we adapt the data-generating process described in Section 6 to include uniform noise $\eta \sim \mathcal{U}(-\Psi^*, \Psi^*)$) added to each of the components of the output $y$.
Accordingly, the approximating model now includes a learnable stochastic variable ($y=f_\psi(x,A) + \epsilon$ with $\epsilon \sim\mathcal{U}(-\Psi, \Psi)$ and $\Psi$ learnable).
The results (reported below for different values of $\Psi^*$) demonstrate that our approach is able to approximate the real distribution even if the processing function is not deterministic.
| Max pert. $\Psi^*$ | MAE on $\theta$ | Max AE on $\theta$ |
| --- | --- | --- |
| 0 | 0.009 $\pm$ 0.001 | 0.06 $\pm$ 0.01 |
| 0.1 | 0.008 $\pm$ 0.001 | 0.05 $\pm$ 0.01 |
| 0.2 | 0.012 $\pm$ 0.001 | 0.06 $\pm$ 0.01 |
| 0.3 | 0.019 $\pm$ 0.003 | 0.09 $\pm$ 0.01 |
| 0.4 | 0.032 $\pm$ 0.003 | 0.13 $\pm$ 0.01 |
- **W3)**
It is indeed possible to parametrize the graph distribution making it input dependent.
One approach involves parameterizing $\theta$, the parameters of $P_A^\theta$, as a function of the input $x$, such as $\theta = g_{\theta'}(x)$, where $\theta'$ denotes an additional set of free parameters. Regarding the theoretical results, Theorem 4.2 can be extended, e.g., to piecewise constant mappings $x \mapsto p(A|x)$; we conjecture that a proof could be established for $p(A|x)$ smoothly varying with respect to $x$.
- **W4)**
Please see our response to Reviewer qZGr's Question 1.
- **W5)**
In the paper, we conducted various experiments to study this theorem's hypothesis, specifically (a) solving the joint learning problem (Section 6.1), (b) setting the processing function to a different, incorrect function (Section 6.2 "Perturbed $f_{\psi^*}$), and (c) using a generic GNN from a different class compared to the true one (Section 6.2 "Generic GNN as $f_{\psi}$"). The empirical evidence gathered demonstrates that, even in these cases, we can still appropriately learn the latent distribution.
Please note that we have also demonstrated that point-prediction loss functions often fail to calibrate the latent distribution, even when the true processing function is used (i.e., $\psi = \psi*$).
**W6**.
We are not sure we have fully understood your proposed solution.
In real-world applications, $P^*(A)$ is unknown and no samples from it are observed. How do you suggest estimating it? Assuming a priori that one model is better than another and, therefore, that it could serve as a ground truth seems inappropriate to us. If our response does not address your comment, could you elaborate in more detail?
Nonetheless, to provide additional evidence that our method learns sensible graph distributions in real-world settings, we run an extra experiment. Please refer to our response "**a (additional experiment)**" to Reviewer qZGr.
**W7**.
Respectfully, we disagree on this point. Kipf et al. (2018) do model the latent relationships as stochastic. Citing from their paper, they use an "encoder that predicts a probability distribution $q_\phi(z|x)$ over the latent interactions given input trajectories", more in detail the encoder "returns a factorized distribution of $z_{ij}$, where $z_{ij}$ is a discrete categorical variable representing the edge type between object $v_i$ and $v_j$". In Section 3.2 they further show how they used the Gumbel-Softmax trick (Maddison et al., 2017) to sample from this discrete latent random variable.
**References**
- Kipf et al. "Neural relational inference for interacting systems.", ICML 2018
- Maddison et al.. "The concrete distribution: A continuous relaxation of discrete random variables.", ICLR 2017
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their rebuttal, it has helped to clarify some aspects of the work better.
I apologize for the mistake I made in my comment on the discussion of (Kipf et al. 2018). I confused this work with the popular (Kipf et al. 2017) GCN paper. Now that I have checked the paper that the authors cited there, it is appropriate to be cited.
However, my question on comparison to existing baselines remain, please allow me to explain in detail how such a comparison can be done on a **synthetic** dataset and correct me if I am wrong.
For the training of this approach, one needs a dataset of features and labels. Now we use the same dataset to train the model in Elinas et al. (https://arxiv.org/pdf/1906.01852 , note that this approach does not need an observed graph for training). After training, we will have the approximation of the graph posterior $p(A|X, Y)$. One can sample several graphs from this distribution and compute various graph statistics. Similarly, from the proposed approach, we can sample several graphs (using the learned $\theta$) after the training is complete and calculate the same statistics.
Now, we would like to know, in which case, these graph statistics are closer to the same statistics of the 'true' graph(s) used to create the dataset. If the empirical calibration offered by this proposed approach is indeed better, it should be reflected in that comparison. In addition, one could compare the performance of these two methods in terms of estimating $y$.
Without these sort of results, my current impression is that a) yes, the numerical experiments verify the theory presented, b) however, there are existing approaches (Elinas et al. ), which operate in the same setting (i.e. estimate the graph distribution and labels together) , c) and, no comparison either in terms of graph estimation and/or label estimation is presented.
Note: Elinas et al. considers a classification setting, but, reading their methodology, extending to the regression setting should not be a major problem.
---
Reply to Comment 1.1.1:
Comment: We appreciate your clarifications, which help us understand and address your comments.
What you requested has been partly implemented already, and we are happy to integrate it.
We performed two additional experiments following your suggestion. The first one compares our methods and implemented baselines (Table 2) with an approach following Elinas et al. (2020).
The second experiment addresses your comment on calibration assessment.
We anticipate that (1) results are consistent with our paper's main argument and (2) considered distributional losses maintain improved calibration performance also according to the approach you proposed.
More in detail:
**Experiment 1.** We trained a model optimizing the ELBO loss in Elinas et al. (2020), adapting it for the synthetic regression task as suggested.
The loss is $\mathcal{L}^{elbo}(\theta,\psi)$ $= - E_{x^*\sim P_x^*}[E_{A \sim P_A^\theta(A)}[ \text{ log }(P^\psi_{y|x^* A}(y^*))]] + KL[P_A^\theta(A)|| \bar{P}_A(A)]$, with prior distribution $\bar{P}_A(A)$ and
$P^\psi_{y|x^* A}(y^*)$ a Gaussian distribution in this case.
We swept through different hyperparameters and choices of the prior $\bar P(A)$, and trained all other parameters $\theta$ and $\psi$ as per Table 2. The overall best results for $\mathcal L^{elbo}$ are as follows:
| Loss | MAE on $\theta$ | MAE on $y$ | MSE on $y$ |
| --- | --- | --- | --- |
| $\mathcal L^{elbo}$ | 0.082 $\pm$ 0.001 | 0.31 $\pm$ 0.01 | 0.19 $\pm$ 0.02 |
| $\mathcal L^{dist}_{\Delta:\text{MMD}}$ | 0.010 $\pm$ 0.002 | 0.269 $\pm$ 0.001 | 0.159 $\pm$ 0.001 |
values for $\mathcal L^{dist}_{\Delta:\text{MMD}}$ are reported from Table 2.
While different hyperparameters yield different tradeoffs between prediction accuracy and model calibration, we observed that the performance is not on par with that achieved using distributional losses.
**Experiment 2.**
To address your request regarding the empirical assessment of model calibration, we compared the learned distributions with the ground-truth one $P_A^*$ with different graph statistics. We considered the input-output pairs from the dataset of Section 6 and the following graph statistics:
| Graph statistic | $P_A^{point}$ | $P_A^{elbo}$ | $P_A^{dist}$ | $P_A^*$ |
| --- | --- | --- | --- | --- |
| Average node degree | $3.28 \pm 0.06$ | $4.12 \pm 0.01$ | $3.166 \pm 0.008$ | $3.120 \pm 0.003$ |
| Average number edges | $39.3 \pm 0.7$ | $49.4 \pm 0.01$ | $37.98 \pm 0.09$ | $37.44 \pm 0.03$ |
| Number of triangles | $9.2 \pm 0.5$ | $8.57 \pm 0.08$ | $6.92 \pm 0.04$ | $6.58 \pm 0.05$ |
In the table:
- $P_A^{dist}$ is learned by optimizing $\mathcal{L}_{\Delta:\text{MMD}}^{dist}$,
- $P_A^{point}$ by optimizing $\mathcal{L}^{point}_{\ell:\text{MSE}}$,
- $P_A^{elbo}$ by optimizing $\mathcal{L}^{elbo}$ from Experiment 1.
Graph statistics were computed from a sample of 500 graphs and repeating the training 3 times. The reported results are consistent with our paper's findings.
Regarding the specific points a), b) and c)
- **Point a)** Indeed this is one of our contributions.
- **Point b)** We agree, and we acknowledge it in our paper; please see from line 046. Further, we performed the additional Experiment 1 described above.
- **Point c) graph estimation** We fulfill this point in two ways. First, we compared the estimated graph distributions in Section 6.3, considering various approaches; specifically, Table 2 considers point-prediction and distributional losses, as well as other losses from the literature. Secondly, we performed the additional two experiments described above, following the reviewer's indications.
- **Point c) label estimation** We do assess the quality of predictions on the target $y$. Our analyses report the accuracy in estimating the expected value of $E_{y^*\sim P^*_{y|x^*}}[y^*]$ and the median median$(y^*)$; please, refer to MSE and MAE on $y$ in Table 2.
To conclude, we believe all three points **a)**, **b)** and **c)** to be resolved now. | null | null | null | null | null | null |
Homophily Enhanced Graph Domain Adaptation | Accept (poster) | Summary: This paper investigates graph domain adaptation through homophily alignment. The authors argued that the graph homophily has been overlooked by existing graph domain adaptation works. To address this issue, the authors first conduct some empirical analyses and find that the homophily discrepancies indeed exist in the widely used benchmarks. Then, the authors proposed a model to use mixed filters to smooth graph signals and align homophily discrepancies between source and target graphs. Experimental results on 5 public datasets show that it can achieve satisfied performance compared with recent baselines.
Claims And Evidence: The key claim is not convincing:
The authors propose to utilize three filters to learn graph signals, which is defined as homophilic filter, full-pass filter and heterophilic filter. Based on the Equations (8), (9) and (10), the authors use $AX$, $IX$ and $LX$ to represent the homophilic, full and heterophilic signals in graph. Why Laplacian matrix $L$ can represent the heterophilic signals, which is contradictive to the graph spectral theory.
Methods And Evaluation Criteria: The evaluation metric is not accurate. As different datasets have different properties, the accuracy (ACC) metric cannot reflect the model’s true performance on these datasets. For instance, MAG dataset’s labels are highly skewed, and macro-F1 score should be used as the evaluation metric. Twitch dataset contains two labels and should use AUC as the evaluation metric.
The model’s design also lacks justification and is contradictive to the graph spectral theory.
Theoretical Claims: I did not carefully check the full proofs in the Appendix due to limited time.
Experimental Designs Or Analyses: Although the authors use 5 different datasets in the experiments, the authors use accuracy for all the datasets, which is not reasonable.
As for the findings, in Figure 2, the authors get the results by using GCN with standard unsupervised GDA setting as evaluation model. However, it is unclear what is the standard unsupervised GDA setting, i.e., MMD or adversarial training.
Supplementary Material: I reviewed the additional experiment parts in the supplementary material.
Relation To Broader Scientific Literature: The key ideas of combining different types of graph signals are not new, which is like multi-view or multi-channel graph convolutional network.
Wang X, Zhu M, Bo D, et al. Am-gcn: Adaptive multi-channel graph convolutional networks[C]//Proceedings of the 26th ACM SIGKDD International conference on knowledge discovery & data mining. 2020: 1243-1253.
Essential References Not Discussed: The authors fail to compare and discuss the following highly relevant papers:
[1] Huang R, Xu J, Jiang X, et al. Can Modifying Data Address Graph Domain Adaptation?[C]//Proceedings of the 30th ACM SIGKDD Conference on Knowledge Discovery and Data Mining. 2024: 1131-1142.
[2] Chen W, Ye G, Wang Y, et al. Smoothness Really Matters: A Simple yet Effective Approach for Unsupervised Graph Domain Adaptation[J]. arXiv preprint arXiv:2412.11654, 2024.
Other Strengths And Weaknesses: Pros:
1. Graph domain adaptation could be a promising application, which helps alleviate distribution shift problem.
2. Experiments are conducted on 5 public datasets including both small- and large-scale datasets.
3. Ablation studies and theoretical analyses are given to show the effectiveness of the proposed model.
Cons:
1. The design of the model needs more justification. The authors propose to utilize three filters to learn graph signals, which is defined as homophilic filter, full-pass filter and heterophilic filter. Based on the Equations (8), (9) and (10), the authors use $AX$, $IX$ and $LX$ to represent the homophilic, full and heterophilic signals in graph. Why Laplacian matrix $L$ can represent the heterophilic signals, which is contradictive to the graph spectral theory.
2. The evaluation metric is not accurate. As different datasets have different properties, the accuracy (ACC) metric cannot reflect the model’s true performance on these datasets. For instance, MAG dataset’s labels are highly skewed, and macro-F1 score should be used as the evaluation metric. Twitch dataset contains two labels and should use AUC as the evaluation metric.
3. The key baselines are missing. More recent baselines should be discussed and compared. Please refer to the reference below [1,2,3].
4. It is not clear how the proposed model enhances the graph homophily. More justification should be given.
5. More ablation studies should be given to show the necessary to adding the representations of $Z_L$, $Z_H$ and $Z_F$.
Reference:
[1] Huang R, Xu J, Jiang X, et al. Can Modifying Data Address Graph Domain Adaptation?[C]//Proceedings of the 30th ACM SIGKDD Conference on Knowledge Discovery and Data Mining. 2024: 1131-1142.
[2] Liu M, Fang Z, Zhang Z, et al. Rethinking propagation for unsupervised graph domain adaptation[C]//Proceedings of the AAAI Conference on Artificial Intelligence. 2024, 38(12): 13963-13971.
[3] Chen W, Ye G, Wang Y, et al. Smoothness Really Matters: A Simple yet Effective Approach for Unsupervised Graph Domain Adaptation[J]. arXiv preprint arXiv:2412.11654, 2024.
Other Comments Or Suggestions: There are too many typos in the paper:
1. Lines 29 to 31, as shown in Figure 1(a), “…ACM3 and ACM4…”. It should be Figure 1(b).
2. Lines 143 to 144, there are two “where”.
3. Lines 190 to 191, “heterophilc” should be heterophilic.
4. Lin3 239, 257, 271, I don’t understand what $H_LH^{l-1}W_L^{l-1}$, $H_FH^{l-1}W_F^{l-1}$ and $H_HH^{l-1}W_H^{l-1}$ mean.
5. In Appendix table 6, the dataset should be Twitch not Twitter.
Questions For Authors: Please refer to the weakness part.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your appreciated feedback. Below, we address the concerns and questions raised in the weaknesses section. Please feel free to reach out if further clarification is required.
# Q1
**Justification:** Our model is designed to separately process graph signals with different levels of homophily. Specifically, we use $AX$ to extract homophilic signals, $IX$ to obtain full-pass signals, and $LX$ to capture heterophilic signals. Furthermore, this design aligns with our theoretical analysis, which shows that the entire model can be optimized by minimizing the distributional shifts of ${D_{\text{KL}}(A^S X^S | A^T X^T)}$, ${D_{\text{KL}}(X^S | X^T)}$, and ${D_{\text{KL}}(L^S X^S | L^T X^T)}$.
**Laplacian matrix $L$:** Regarding $L$, There might be some misunderstanding. In fact, the graph **Laplacian matrix can be viewed as a high-pass filter that obtains heterophilic signals**—a perspective that has been adopted in several existing works [1, 2, 3] (e.g., in Section2.1 of [1], it says "To address the heterophily challenge, high-pass(HP) filter $L$ is often used to replace low-pass(LP) filter $A$"). To the best of our knowledge, we are unaware of any graph theory that contradicts utilizing a Laplacian matrix to obtain heterophilic signals. We are pleased to provide more clarification and havea more detailed discussion with you regarding this matter if you still have concerns.
[1] Luan S, Hua C, Xu M, et al. When do graph neural networks help with node classification? Investigating the homophily principle on node distinguishability. Advances in Neural Information Processing Systems, 2023.
[2] Luan S, Hua C, Lu Q, et al. Revisiting heterophily for graph neural networks. Advances in neural information processing systems, 2022.
[3] Li B, Pan E, Kang Z. Pc-conv: Unifying homophily and heterophily with two-fold filtering. Proceedings of the AAAI conference on artificial intelligence. 2024.
# Q2
Thanks for your constructive comment! Following your suggestion, we also conducted additional experiments, evaluating **MAG** using macro-F1 and **Twitch** using AUC to address your concern. Due to word limitations, we have provided visualizations of these tables in the supplementary material, accessible via the following link [MAG](https://files.catbox.moe/e1ppdo.png) and [Twitch](https://files.catbox.moe/rw69ik.png).
# Q3
We acknowledge the importance of comparing our approach with recent advancements, including TDSS, A2GNN, GraphAlign [1*,2*,3*]. We report the performance of HGDA and the baseline methods on the [Airport, ACM, Blog](https://files.catbox.moe/hnbk9e.png) and [Citation](https://files.catbox.moe/or0weu.png) datasets. For the results on **MAG** and **Twitch**, please refer to our response to **Q2**. Our results demonstrate that while their method performs well, our approach exhibits **outperformance**, highlighting the importance of minimizing homophily shift. In future version, we will include these baseline methods along with additional evaluation metrics.
# Q4
Thank you for your valuable comment. We believe there might be a slight misunderstanding regarding the notion of "enhancing graph homophily" in the context of our work. Our paper does not aim to improve or increase the inherent homophily of the graph itself. Instead, our focus is on highlighting the homophily shift that occurs between the source and target domains in graph domain adaptation (GDA), and proposing a method to mitigate this shift. We will further revise our paper to clarify this point. Regarding the justification on this point, we provide [experimental results](https://files.catbox.moe/egsaqz.png) that report the classification accuracy on target graph subgroups with varying levels of homophily. The results show that **$HGDA_L$** performs best in subgroups with high homophily, **$HGDA_F$** performs best in subgroups with intermediate homophily, and **$HGDA_H$** performs best in subgroups with low homophily. These findings underscore the effectiveness of our method, which employs a combination of filters to mitigate homophily discrepancies at various levels.
# Q5
Regarding the concern about **$Z_L$**, **$Z_F$**, and **$Z_H$**, we would like to clarify that these embeddings are obtained by applying homophilic, full-pass, and heterophilic filters, respectively. In **Table 1**, **Table 2**, and **Table 3**, the variants **$HGDA_L$**, **$HGDA_F$**, and **$HGDA_H$** exclusively utilize **$Z_L$**, **$Z_F$**, and **$Z_H$**, respectively. The results of the main experiments show that each variant performs differently across datasets, which we attribute to the intrinsic homophily distribution characteristics of each dataset. The effects of **$Z_L$**, **$Z_F$**, and **$Z_H$** are further demonstrated by the experiments discussed in **Q4**.
For clarification, the GCN baseline under the standard unsupervised GDA setting employs a two-layer GCN architecture combined with an MMD loss for domain alignment.
---
Rebuttal Comment 1.1:
Comment: Dear authors,
Thank you for your rebuttal. However, it seems that the links you provided are no longer valid. Could you please check and share the updated links?
---
Reply to Comment 1.1.1:
Comment: We apologize for any inconvenience and are pleased to provide valid links to clarify our rebuttal. Specifically, we have included links corresponding to each question, hosted on Google Docs, Anonymous GitHub, and imgbb, which can be found in Q2, Q3, and Q4 of the rebuttal, respectively.
# Q2
Google Docs: [MAG](https://docs.google.com/document/d/1f04LxgLsOYilN6iBnTJZhkbQvscgBw1xxrUIE80SDXc/edit?usp=sharing) [Twitch](https://docs.google.com/document/d/1qY1O26L7pm8wuGEZ6vPToSONZD_-AJsKLJkMRt05-PA/edit?usp=sharing)
Anonymous GitHub: [MAG](https://anonymous.4open.science/r/ICMLrebuttal-B40A/MAG_%20F1.png) [Twitch](https://anonymous.4open.science/r/ICMLrebuttal-B40A/Twitch_auc.png)
imgbb: [MAG](https://ibb.co/qY94XPdG) [Twitch](https://ibb.co/hRkXxc3p)
# Q3
Google Docs: [Airport, ACM, Blog](https://docs.google.com/document/d/192-_ziiSFqO0J9ct9kgwFWAAqJAXlGo_2ZEjdBmPl7U/edit?usp=sharing) [Citation](https://docs.google.com/document/d/14tlIaq5X6SebK_eh-NMvYNssfBLjboH0bCwUH29n5TQ/edit?usp=sharing)
Anonymous GitHub: [Airport, ACM, Blog](https://anonymous.4open.science/r/ICMLrebuttal-B40A/Airport,%20ACM,%20Blog.png) [Citation](https://anonymous.4open.science/r/ICMLrebuttal-B40A/Citation.png)
imgbb: [Airport, ACM, Blog](https://ibb.co/jXr63Kk) [Citation](https://ibb.co/wZdjB7NR)
# Q4
Google Docs: [experiment results](https://docs.google.com/document/d/1l_IBf_05Ipy8UED84cpLds5hT2Mp-LlIMd1e8DoTQZM/edit?usp=sharing)
Anonymous GitHub: [experiment results](https://anonymous.4open.science/r/ICMLrebuttal-B40A/experiment%20results%20homophily%20ratio.png)
imgbb: [experiment results](https://ibb.co/HT5frDtq)
We would be grateful if this could improve your understanding of our works. We would be pleased to include these HGDA results on these baseline methods, additional evaluation metrics, and other improvements in our future revision. | Summary: This paper proposes a novel Graph Domain Adaptation algorithm which solves graph homophily disparity for effective domain alignment. It shows that homophily distribution shifts exist wildly in GDA datasets and could damage GDA performance in both empirically and theoretically ways. Inspired by theoretical results, it also provides a method to mitigate this discrepancy through cross-channel homophily alignment (HGDA).
Claims And Evidence: The paper claims that homophilic ratio divergence exhibits a negative correlation with the classification accuracy of target graph nodes. It provides empirical results in Figure 2, which contain target node classicifaction accuracy percent difference and homophily distribution shift in each corresponding subgroups.
Methods And Evaluation Criteria: While most aspects of the evaluation are comprehensive, with performance reported over eight recent baselines on six datasets, the evaluation benchmark is partially limited. For benchmark Twitch [1], Russia (RU) and Spain (ES) are not involved. I also want to see the HGDA performance in ogbn-arxiv[2], which involves temporal discrepancy with different publication years.
[1] Liu M, Fang Z, Zhang Z, et al. Rethinking propagation for unsupervised graph domain adaptation[C]. AAAI 2024
[2] Liu M, Zhang Z, Tang J, et al. Revisiting, Benchmarking and Understanding Unsupervised Graph Domain Adaptation[J]. NeurIPS 2024
Theoretical Claims: This paper theoretically justifies the impact of a homophily distribution shift on GDA and demonstrates that this discrepancy can be mitigated by addressing the homophilic and heterophilic signals.
Experimental Designs Or Analyses: I check the validity of experiments, consisting of performance comparison, ablation study, and hyper-parameter and model efficient experiment analysis.
Supplementary Material: I review the supplementary material, including empirical study in other datasets, model parameter analysis, and model efficient experiment.
Relation To Broader Scientific Literature: This paper provides a novel view on GDA tasks. Its method has theoretical guarantees. Although SA-GDA[1] is partially similar to HGDA in utilizing graph signal in spectral space, I recommend that the authors discuss their differences with that paper in related work.
Essential References Not Discussed: To my knowledge, the paper discusses the most essential references.
Other Strengths And Weaknesses: Strengths:
1.This paper presents a well-founded study supported by both theoretical analysis and experimental evidence.
2.The method proposed in this paper is grounded in meaningful theoretical research.
Weaknesses:
1.The experimental evaluation in this paper is somewhat limited. As noted in the Evaluation Criteria, a more comprehensive experiment across additional datasets would strengthen the study and improve its validity.
2.The dotted line in the two sub-graphs of Figure 1 represents the overall graph node homophily ratio. However, the paper does not clearly explain the method used to calculate this value.
3.Can the authors clarify the impact of the three proposed alignment modules, namely ${\text{KL}}(Z_L^S \| Z_L^T)$, ${\text{KL}}(Z_H^S \| Z_H^T)$, and ${\text{KL}}(Z_F^S \| Z_F^T)$, on the classification performance of nodes with different homophily ratios? Intuitively, these modules should play distinct roles in the alignment process.
4.Why is ${D_{\text{KL}}(P_S^H \| P_T^H)} $, one of the terms in Theorem 1, considered a fixed value? Additionally, why is it not subject to optimization?
Other Comments Or Suggestions: In Table 1, a vertical line between the Airport and ACM datasets appears to be missing.
Questions For Authors: Additional experiments, particularly on the ogbn-arxiv dataset, would help validate HGDA's performance in addressing temporal discrepancies. Furthermore, a running time analysis and comparisons with a broader set of baseline models are needed to strengthen the evaluation. Other questions refer to other strengths and weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your constructive feedback! Below, we address the concerns and questions raised in the weaknesses section. Please feel free to reach out if further clarification is required.
# Q1
Thanks for your constructive comment! Following your suggestion, we also conducted [additional experiments](https://files.catbox.moe/ewkc85.png), evaluating HGDA performance on **ogbn-arxiv** dataset. Specifically, we report the performance of HGDA on three tasks. As for ogbn-arxivl networks, we choose the year to separate networks, which are collected from **1950-2016(50-16), 2016-2018(16-18), and 2018-2020(18-20)**. As for Twitch **RU and ES**, we are pleased to provide their experiment, which is as [follows link](https://files.catbox.moe/9hxty1.png). Our results demonstrate that while their method performs well, our approach exhibits **outperformance**, highlighting the importance of minimizing homophily shift. In future versions, we will include these baseline methods along with additional evaluation metrics.
# Q2
We apologize for any misunderstanding caused by the previous lack of clarity. To clarify, overall graph node homophily ratio is $\; \int_{0}^{1} v \,\cdot\, H^v_{\text{node}} \,\mathrm{d}v.$
which actually is our **Definition 1 (Graph-Level Node Heterophily Distribution)** in **Section3.3**. This method computes the homophily distribution across the entire graph. As shown in **Fig. 1**, in the Airport dataset, while the overall graph-level node heterophily distributions of the BRAZIL and EUROPE subgraphs are relatively similar, significant differences exist in the local homophily subgroups. These observations highlight the need for our model to handle homophily shifts effectively at different levels.
# Q3
To address your concern, we provide [experimental results](https://files.catbox.moe/egsaqz.png) that report the classification accuracy on target graph subgroups with varying levels of homophily. We also provide [synthetic experiments](https://files.catbox.moe/9odyw2.png) to validate the effectiveness of our three filter pairs in addressing varying levels of homophily shift, which detail can be found in **Reviewer BNmW** in **Q4**. The results show that **$HGDA_L$** performs best in subgroups with high homophily, **$HGDA_F$** performs best in subgroups with intermediate homophily, and **$HGDA_H$** performs best in subgroups with low homophily. These findings support the effectiveness of our method in aligning graph signals across different levels of homophily. Therefore, we can conclude that these three modules provide different roles in HGDA.
# Q4
Regarding **Definition 1 (Graph-Level Node Heterophily Distribution)**, $P_G^H$ captures structural information inherent to the graph, as observed in nature [1, 2]. Consequently, unless the graph topology itself is directly altered, $P_G^H$ remains a fixed quantity. As a result, ${D_{\text{KL}}(P_S^H \| P_T^H)}$ is also an intrinsic and fixed value. Following your suggestion, we will address these concerns and provide clarification in a future version of the paper.
[1] Pan E, Kang Z. Beyond homophily: Reconstructing structure for graph-agnostic clustering. International conference on machine learning. , 2023.
[2] Xie X, Chen W, Kang Z. Robust graph structure learning under heterophily. Neural Networks, 2025.
Thank you for your comment regarding Table line problems. We apologize for this and have carefully reviewed and corrected them throughout the paper in the future version.
---
Rebuttal Comment 1.1:
Comment: I appreciate the rebuttal, and it addresses my concerns regarding the usefulness of the results. After seeing the discussion in the rebuttal, I am leaning toward accepting this paper. Please ensure the additional datasets HGDA results are also included in the final manuscript.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer,
Thank you very much for your thoughtful and constructive feedback. We sincerely appreciate your time and effort in reviewing our work. We will include the HGDA results on the additional datasets, along with the other improvements, in our future revision. We are grateful for your positive evaluation, and we would truly appreciate it if you could consider reflecting this in your final score.
Sincerely,
The Authors | Summary: This paper studies the problem of Graph Domain Adaptation problem through analysis homophily shift. This study reveals that homophily distribution shift negatively influences target domain accuracy in an empirical study. Empirical study reveals that homophily discrepancy exists in many benchmarks and provides an essential role in GDA. Through theoretical analysis using the PAC-Bayes framework, the authors prove that the domain shift is bounded by graph homophily distribution shift. Moreover, their theoretical analysis shows that homophily shift can be mitigated through aligning different signals. The authors conducted comprehensive experiments to validate the algorithm's performance with a sufficient number of baseline methods compared.
Claims And Evidence: Yes. The claims made in the submission are generaly supported by both theoretical and experimental evidence.
Methods And Evaluation Criteria: Yes. The proposed method make sense in reducing graph homophily discrepancy and the experimental evaluation appears reasonable and is conducted using widely accepted criteria.
Theoretical Claims: Yes. I have reviewed the proofs of the theoretical claims in the paper in the supplemental material particular for Theorem 1.
Experimental Designs Or Analyses: The exoerimental designs are generally sound whicn include the ablation study and parameter analysis.
Supplementary Material: Yes. I have check the proof and the additional experiment in the supplementary material.
Relation To Broader Scientific Literature: The key contributions of the paper are related to the filed of graph domain adaptation and the homophily shift is of particular studied.
Essential References Not Discussed: Some recent advancements in GDA might also need to cite, such as those discussed in [1].
[1] Zhang, Zhen, et al. "Aggregate to Adapt: Node-Centric Aggregation for Multi-Source-Free Graph Domain Adaptation.'' *The Web Conference*, 2025
Other Strengths And Weaknesses: Strengths:
- This paper highlights the importance of homophily distribution discrepancy in GDA and empirically investigates its impact on GDA performance.
- This paper is technically sound and novel. In theoretical analysis part, it demonstrates that the heterophily distribution shift between the source and target graphs can mitigate through homophilc signal, graph attribute signal, and heterophilic signal.
- HGDA method is theoretically motivated and aligns the three graph signals using KL divergence, ensuring consistency with the theoretical findings.
- The experiments are convincing and the experiment details are complete with detailed experiment description in the supplemental material.
Weaknesses:
- The explanation of the relationship between the proposed method and Theorem 1 in Section 4.2 could be clarified, particularly regarding their differing motivations.
- The paper should expand the discussion in the related work section to include connections to other studies that address structural shift in GDA. Since homophily is fundamentally a structural property, drawing parallels with existing approaches to structural shift could provide a broader contextual foundation for the study.
- Although the paper has generally sufficient experimental data set, it could benefit from additional experiments on other benchmarks for GDA’s target node classification task, e.g., ogbn-arxiv.
Other Comments Or Suggestions: Typos:
- Line 282 "Alignemnt"
- Line 98 "homophilc"
Questions For Authors: See the weakness above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your feedback. We would also appreciate your agreement on our method's novelty and effectiveness. Below, we address the concerns and questions raised in the weaknesses section. Please feel free to reach out if further clarification is required.
# Q1
$ KL(Z_L^S \| Z_L^T) $ aligns the homophilic signal, corresponding to the term $ D_{\text{KL}}(A^S X^S \| A^T X^T) $. Similarly, $ KL(Z_H^S \| Z_H^T) $ directly aligns the graph attributes, corresponding to the term $ D_{\text{KL}}(X^S \| X^T) $. Finally, $ KL(Z_F^S \| Z_F^T) $ aligns the heterophilic signal, which is consistent with the term $ D_{\text{KL}}(L^S X^S \| L^T X^T) $ in **Theorem 1**. Specifically, this can be explained as follows. The term ${D_{\text{KL}}(A^S X^S | A^T X^T)}$ quantifies the divergence in the graph homophily signal, capturing how graph attributes—modulated by the adjacency matrices—differ between the source and target graphs. In contrast, ${D_{\text{KL}}(X^S | X^T)}$ measures the divergence in the distribution of graph attributes between the two domains. Lastly, ${D_{\text{KL}}(L^S X^S | L^T X^T)}$ quantifies the divergence in the graph heterophilic signal, where the attributes are modulated by the graph Laplacian matrix.
# Q2
Some early works have addressed graph homogeneity through reconstruction [1] to enhance graph homophily, our work does not directly modify the graph structure due to the computational complexity involved. Instead, **our method focuses on processing homophilic information at varying levels by grouping nodes accordingly**. Inspired by theoretical insights, the model employs low-pass, full-pass, and high-pass filters to capture homophilic signals at different levels. We are pleased to discuss these topics in the related work section of the future version.
[1] Pan E, Kang Z. Beyond homophily: Reconstructing structure for graph-agnostic clustering. International conference on machine learning. , 2023.
# Q3
Thanks for your constructive comment! Following your suggestion, we also conducted [additional experiments](https://files.catbox.moe/ewkc85.png), evaluating HGDA performance on ogbn-arxiv dataset. Specifically, we report the performance of HGDA on three tasks. As for ogbn-arxiv networks, we choose years to separate networks, which are collected from **1950- 2016 (50- 16), 2016- 2018 (16- 18), and 2018- 2020 (18- 20)**. Our results demonstrate that while their method performs well, our approach exhibits **outperformance**, highlighting the importance of minimizing homophily shift. We will include these baseline methods and additional evaluation metrics in future versions.
Thank you for your comment regarding typo problems. We apologize for this and have carefully reviewed and corrected them throughout the paper in the future version. | Summary: This paper investigates the graph domain adaptation (GDA) problem highlighting the importance of handling the shift across graph homophily distribution between the source and target graphs. They motivate the issue from both the empirical aspect and from theoretical analysis. Empirically, it has been observed that distinct proportion of different homophily subgroups across the source and target graph will impact the target performance. Theoretically, they show an error bound in terms of homophilic signal shift, heterophilic signal shift, node feature shift and node heterophily distribution shift. To handle the shifts, they propose the algorithm HGDA that align three types of signal shifts using KL divergence together with with source classification loss and target entropy loss. They evaluate the variants of HGDA with DA and GDA baselines on wide range of real world datasets.
Claims And Evidence: **Strength:**
- Novel shift consideration: focusing on the homophily of subgroups and the entire distribution of node homophily is an interesting and valuable direction in addition to previous GDA works.
- Empirical justification: The figure 1/7 justify that this type of shift in node homophily exist in the real world datasets. Figure 2/8 try to demonstrate the empirical performance for subgroups with different homophily ratio against distinct homophily divergence.
**Question/Weakness:**
- It is good that you include Fig 5 as a comparison to Fig 2 after adopting the proposed method. It seems that after HGDA, we have a balance performance with different subgroups instead of related to the level of homophily divergence in fig 2. Can you elaborate more on why your method can handle different divergence level well?
Methods And Evaluation Criteria: **Strength:**
- The method itself is easy to follow and use
- The method design generally follows the motivation, empirical and theoretical analysis
**Weakness/Questions:**
- The method primarily focus on feature alignment which might be suboptimal in terms of graph data
- There is no specific and explicit handle that might target different levels of homophily divergence, i.e. the fourth term in the theoretical analysis. Although it appears to be an intrinsic graph parameter, but it might be able to handle empirically under GNN since it is a main part of your motivation saying this divergence causes performance degradation.
- Potentially lack control on how to determine the importance of homophilic/heterophilic alignment, should that depend on the distribution of the node homophily? Also, rather complicated loss for training.
- How this method can handle covariate shift, label shift and conditional structure shift that are previously discussed in GDA literatures? How you position homophily shift with previous discussed shifts and literature.
Theoretical Claims: The theoretical analysis tends to largely rely on results from previous works with limited contribution in novelty. Also, the analysis regarding KL divergence decomposition of feature distributions tends to be oversimplified and the bound seems to be not tight.
Experimental Designs Or Analyses: **Strength:**
- Compared to many baselines and real world datasets
- Include some visualizations and analysis over parameters and different variants
**Weakness:**
- No indication of repeated experiments and no standard deviation included in the results
- Lack analysis in the three variants: For instance, in principle, $HGDA_F$ does not use graph information and should have similar results with DANN, but why it can have better results than graph-based methods and have comparable results with the other two variants?
- Better if you can provide some synthetic experiments or more detailed analysis over real datasets that detailing how HGDA handle different types/levels of shift
Supplementary Material: Briefly went over the proof, plots and the algorithm.
Relation To Broader Scientific Literature: This paper helps bring up another issue that exist in GDA
Essential References Not Discussed: This paper includes a wide range of relevant literatures but could elaborate more on how their problem and method compared to previous literature.
Other Strengths And Weaknesses: Please refer to the above sections
Other Comments Or Suggestions: some typos: "Alignemnt"->"Alignment" in subtitle 4.2 and page 6 line 282
Questions For Authors: - Question regarding Fig.2: There seems to be a consistent gap between the two accuracy lines indicating two adaptation directions. Your plot shows that the accuracy only relates to the absolute gap in homophily distribution divergence but not with the directions. Can you explain why this is the case? Also, regarding the consistent gap between adaptations from two directions, if it is not attributed to the homophily distribution, what can be the potential cost? e.g. E & B has a large gap in (c) and A3 & A4 has a small gap.
- Question regarding training: How is the loss converge during training since we have a rather complex loss terms with many terms? Why choosing KL divergence in particular to align the distribution of filtered signals.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your feedback. We would also appreciate your agreement on our method's novelty and effectiveness. Below, we address the concerns and questions raised in the Claims And Evidence, Weaknesses, Theoretical Claims, and Questions For Authors section. Please feel free to reach out if further clarification is required.
# Q1
As shown in Fig. 5, HGDA achieves balanced performance across different subgroups by processing graph signals with varying levels of homophily through three specialized filters. Specifically, **$HGDA_L$** performs well in homophilic subgroups, **$HGDA_H$** excels in heterophilic subgroups, and **$HGDA_F$** is most effective in subgroups with intermediate homophily levels. The combined contributions of these components lead to an overall balanced performance.
# Q2
1. We acknowledge that continued research into graph-structured data will further enhance the effectiveness of such approaches. However, HGDA method incorporates both homophilic and heterophilic filters that leverage the structural information of the graph.
2. Our motivation is to address subgroups with varying levels of homophily. To this end, we employ a homophilic filter to extract subgroups with **high homophily**, a full-pass filter for those with **middle homophily**, and a heterophilic filter for subgroups with **low homophily** [1]. This behavior can be observed in Fig. 5. As stated in **Theorem 1**, ${D_{\text{KL}}(P_S^H | P_T^H)}$ cannot be directly optimized as shown in **Definition1**. However, we can instead minimize the divergence of different homophily-level signals by optimizing ${D_{\text{KL}}(A^S X^S | A^T X^T)}$, ${D_{\text{KL}}(X^S | X^T)}$, and ${D_{\text{KL}}(L^S X^S | L^T X^T)}$, thereby alleviating homophily divergence.
3. In this paper, we focus on addressing the challenge of homophily shift. We acknowledge that covariate shift, label shift, and particularly conditional structure shift are also critical issues related to homophily in graph domain adaptation (GDA), which we plan to explore in future work.
# Q2
As noted in **Appendix B**, each experiment was repeated five times, and the reported results represent the average performance. Additionally, we will include the standard deviation of the results in future versions of the paper.
# Q3
The key difference between **$HGDA_F$** and **DANN** lies in their alignment strategies: $HGDA_F$ employs a KL divergence-based alignment loss, whereas DANN uses an adversarial loss. Moreover, DANN does not incorporate the pseudo-label classification loss on the target graph, which is included in our approach. These differences likely account for the performance gap observed between the two methods. Overall, the performance of different HGDA variants is related to the underlying distribution of the dataset. Specifically, in this [experiment](https://files.catbox.moe/egsaqz.png), **$HGDA_L$** and **$HGDA_F$** tend to perform better on datasets with a higher proportion of homophilic subgroups, while **$HGDA_H$** and **$HGDA_F$** perform better on datasets with a relatively higher degree of heterophily. In the meanwhile, we really appreciate your question, which gives us the opportunity to further improve our manuscript. Specifically, in light of your comments, we will revise **Section 5.3** to further clarify our motivation and avoid potential confusion.
# Q4
We provide [synthetic experiments](https://files.catbox.moe/9odyw2.png) to validate the effectiveness of our three filter pairs in addressing varying levels of homophily shift. Specifically, we randomly generated five sets of source and target graphs, each containing 300 nodes, where the homophily properties for each subgroup were varied in increments of 0.01. In the picture, the horizontal axis denotes the various homophily subgroups of target graphs, and the vertical axis indicates the performance of different HGDA variants across these homophily levels. The results indicate that $HGDA_L$ performs best in high-homophily scenarios, $HGDA_F$ excels in medium-homophily settings, and $HGDA_H$ is most effective in low-homophily contexts.
# Q5
We would like to further clarify that, as demonstrated in **Theorem 1**, the performance differences between source and target domain adaptation are influenced not only by component $\sqrt{D_{\text{KL}}(P_S^F \| P_T^F)}$, but also by component **$ L^\gamma_S(\phi)$**. Moreover, the effectiveness of **$L^\gamma_S(\phi)$** across different adaptation tasks also **depends on the source domain's empirical risk, which indicates an accuracy gap between two adaptation directions**.
# Q6
The use of KL divergence in our loss function is theoretically motivated. Additionally, incorporating these three loss terms does not significantly increase computational overhead. The overall computational complexity of HGDA remains controlled at **$O(N^2 \cdot d)$**.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response, it addressed some of my questions so I will raise my score to 3.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer,
Thank you for your thoughtful feedback and for increasing the score of our manuscript. We sincerely appreciate your insightful questions, as addressing and clarifying them has significantly strengthened our paper.
Sincerely,
The Authors | null | null | null | null | null | null |
TGDPO: Harnessing Token-Level Reward Guidance for Enhancing Direct Preference Optimization | Accept (poster) | Summary: Recent work in RLHF has revealed the benefits of utilizing fine-grained rewards. The combination of token-level guidance with DPO, however, remains to be explored.
To address this challenge, this paper decomposes the sequence-level RL formulation in the original DPO derivation as a sequence of token-level RL problem, from which closed-form solution for the optimal token-level policy and reward can be derived.
From this, this paper derives a loss with token-level reward guidance for DPO and proposes a practical reward guidance based on the induced DPO reward.
This formulation enables different tokens to exhibit varying degrees of deviation from reference policy.
Claims And Evidence: Yes, the empirical performance validates the proposed method.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes, tested on standard RLHF benchmarks
Supplementary Material: Yes
Relation To Broader Scientific Literature: See the Strength section.
Essential References Not Discussed: See the Weaknesses section
Other Strengths And Weaknesses: ## Strengths
1. Dense/token-level reward is a promising direction for RLHF to improve upon the classical bandit/sequence-level formulation. The combination of this direction with DPO is particularly less cultivated.
2. The proposed method shows competitive performance gain.
## Weaknesses
1. The idea of "token-level reward guidance + DPO" has been explored, e.g., in [1, 2]. Specially, Equ. (8) in this paper is almost identical to Equ. (12) in [1]. The authors need to properly discuss the connection and novelty compared to these prior works.
2. Some of the basic terms/concepts are confused with others, see the next "Suggestions" section.
3. Please check the Questions section for a potential mistakes on the Method section and several unclear parts.
***
[1] A Dense Reward View on Aligning Text-to-Image Diffusion with Preference. In ICML 2024.
[2] Earlier Tokens Contribute More: Learning Direct Preference Optimization From Temporal Decay Perspective. In ICLR 2025.
Other Comments Or Suggestions: 1. "sentence-level reward" is not accurate, what the authors refer to should be termed as bandit/{sequence, trajectory, response}-level reward, since each response may contain multiple sentences, for example, in the summarization task. Ditto all presence of "sentence".
2. Most of the appearance of "proximal policy optimization problem"/"PPO problem" should be changed to "KL-regularized policy optimization"/"KL-regularized RL"/"KL-regularized control".
Questions For Authors: 1. Could you explain what is "sentence-level proximal policy optimization with token-level reward guidance"? In particular, why is PPO sentence-level given that the reward is token-level?
2. In Assumption 4.2:
- What is "the **corresponding** dense token-level reward"? Why does the reward need to be learnt to correspond to the policy?
- What is the different between $\hat r$ and $r_\phi$? Why couldn't we optimize $\pi_\theta$ against $\hat r$?
- What is the requirement of the function $f$? The current description looks like a constant function of 1 is also valid, which will trivialize Equ. (10). For the proof of Equ. (15), I believe we need the stronger assumption of $\epsilon \times M \times T_w \approx 0$.
3. What is the benefit of introducing $f(\hat r)$ in Equ. (10)? See the following question for a problem with the current specification of $f$.
4. L286: "likely to make this token as a dispreferred one" --- this is incorrect. The current loss will only make the optimization strength of those token relatively smaller, rather than minimizing their likelihood, since Assumption 4.2 says $|f(u)| \geq 1 - \epsilon > 0$ for small $\epsilon$. Ditto L299. With this, the author may need to revise the claim in L406-408 about "reduces conflicts".
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1 Comparison with existing works**
All [1], [2] and ours are based on the assumption of dense token-level reward to derive respective DPO loss functions. Eq. (8) in our work seems similar to Eq. (12) in [1], but our Eq. (8) is not solvable since $s_t\sim\mathcal{D}\_t$ is dependent on the policy $\pi\_{\theta}$ to be optimized. This has been demonstrated in line 219 (left) - line 168 (right) of the main text. In the final version we will give citations, discuss connections with [1, 2] and the differences highlighted as follows:
**Motivation Differences:** We intend to incorporate a learned token-level reward explicitly into DPO. While, they only focus on asigning more weight on earlier tokens.
**Loss Function Differences:** Our work explicitly incorporate an existing token-level reward in the loss function for guiding DPO. [1] uses the same loss as DPO and modifies the sampling probability for different diffusion timesteps. [2] adds a temporal decay factor for each token in the DPO loss. Their loss functions do not leverage token-level reward.
**Method Differences:** Integrating token-level reward in DPO's loss function explicitly presents distinctive difficulties, especially in the derivation. Thanks to all reviewers' comments, we have proposed a new approach for canceling partition functions in the Bradley-Terry model, please see **Q7**.
[1] A Dense Reward View on Aligning Text-to-Image Diffusion with Preference
[2] Earlier Tokens Contribute More: Learning Direct Preference Optimization From Temporal Decay Perspective
**Q2 Accurate word choice**
We will change to use "response-level reward" and "KL-regularized policy optimization" to improve accuracy.
**Q3 Explain "sentence-level PPO with token-level reward guidance"**
A sequence of dense token-level reward $r_{\phi}(s_t, a_t)$ is obtained before PPO, and then it can guide PPO finetuning in a more fine-grained way.
**Q4 What is the corresponding dense token-level reward**
Actually, $\pi_{\hat\theta}$ does not necessarily relate to $\hat{r}$ in Assumption 4.2. $\pi_{\hat\theta}$ is only used for sampling $s_t$ in Equation (10). Now, the first sentence of Assumption 4.2 is modified as: Suppose we have learned a dense token-level reward $\hat{r}$ using some effective learning approach. In the revision, we will improve the description and notation to reduce misunderstanding.
**Q5 Difference between $\hat{r}$ and $r_{\phi}$**
$\hat{r}$ is an existing dense token-level reward, used for shaping the reward $r_{\phi}$ in Equ. (10). Following the derivation of DPO, $r_{\phi}$ is expressed with $\hat r$, $\pi_{\theta}$ and $\pi_{\text{ref}}$ by solving Equ. (10). And finally, $\hat{r}$ will appear in Equ. (16) of our loss function, but $r_{\phi}$ does not.
If we optimize $\pi_\theta$ against $\hat r$, then Equ. (10) becomes
$$
\max_{\pi_{{\bf\theta}}} \mathbb{E}\_{s_t\sim\hat{\mathcal{D}}\_t, a_t\sim \pi_{\theta} (\cdot|s_t) } \left[{r_{\phi}(s_t, a_t)} - {\beta f(\hat{r}(s_t, a_t))}\log \frac{ \pi_{\theta} (a_t|s_t)}{\pi_{\text{ref}}(a_t|s_t)}\right].
$$
We tried and found it is difficult to solve the problem due to the expectation on the product term.
**Q6 Requirement for $f$**
In Assumption 4.2, the $f$ satisfying $f(0)=1$ and $|f(u)-1|\le\varepsilon$ is sufficient for deriving our TGDPO. Concrete $f(u)$ can be chosen by developers personally. As for us, Equ. (17) is adopted in our experiments. If $f(u)\equiv 1$ then our TGDPO degenerates to DPO, which is not interesting.
**Q7 Strong assumption for Equation 15**
Thank you very much for the comment! Now the assumptions have been completely removed, the approach is novel. The theorem and proof can be seen in response to **Q3 of Reviewer F88J**. We will provide revisions in the final version.
**Q8 Benefit of introducing $f(\hat r)$ in Equ. (10)**
The benefit of introducing $f(\hat r)$ in Equ. (10) is in Equ. (16) of the loss function.
We adopt Equ. (17) in our experiments. Then take win response $y_w$ for an example, the other is similar. In Equ. (16),
$$
f(\hat{r}([x, y_w^{<t}], y_w^t)) \log\frac {\pi_{\theta} (y_w^t|[x, y_w^{<t}])}{\pi_{\text{ref}}(y_w^t|[x, y_w^{<t}])} = (1 + \alpha \hat{r}([x, y_w^{<t}], y_w^t)) \log\frac {\pi_{\theta} (y_w^t|[x, y_w^{<t}])}{\pi_{\text{ref}}(y_w^t|[x, y_w^{<t}])}.
$$
For $\hat{r}([x, y_w^{<t}], y_w^t)>0$, we emphasize more on this token, otherwise less or keep the weight unchanged as 1.
**Q9 Improper description in L286, L406-408**
Thank you very much for pointing out the issues. We modify them as:
1) L283-286 (right): "Then this token is optimized with less strength during the optimization of the loss function $\mathcal{L}\_{\text{TGDPO}}(\pi_{\theta})$, since $f(\hat{r}([x, y_w^{<t}], y_w^t)) <1$."
2) L296-299 (right): Similar to point 1.
3. L406-408 (left): "distinguish preferred tokens in chosen samples and dispreferred tokens in rejected
ones, TGDPO takes care of them and enables ..." | Summary: This paper proposes a method that integrates Direct Preference Optimization (DPO) with token-level rewards. The paper first provide an upper bound for rewards in sentence-level LLM generation by decomposing the problem into a series of token-level reward maximization tasks. Building on this foundation, the paper adapts the DPO method to solve these token-level reward-maximization problem. Experiments were conducted on three models and evaluated across three benchmarks. The results demonstrate that the proposed method outperforms baseline approaches.
Claims And Evidence: In this paper it is claimed that the proposed TGDPO performs better than baselines like DPO and SimPO. This is adequately supported by experiments in Section 5 of this paper.
Methods And Evaluation Criteria: The paper mainly focuses on RLHF problem. The evaluation benchmark involved, namely AlpacaEval, MT-Bench and Arena-Hard, are all widely used benchmarks for alignment evaluation.
Theoretical Claims: The concerns regarding methodology are listed below
1.While Theorem 4.1 appears to be correct, its intended message is unclear. The objective in equation (8) can certainly serve as an upper bound for equation (2), but there is no guarantee that a policy maximizing (8) will also maximize (2). To be more specific, it looks like the objective in equation (8) is to myopically optimize the reward of the currect step without considering further states. However, in RL, the goal is to maximize the expectation of **total** future rewards (i.e., Q-function). policy that optimizes one-step rewards might lead the agent into unfavorable states, ultimately hindering its ability to achieve high cumulative rewards.
2. The introduction of function $f$ in Assumption 4.2 appears insufficiently motivated. Could the authors provide further explanation and justification for its inclusion?
3. In equation 15, the $\approx$ is obtained by assuming $Z(x, y_w^{<t}) \approx Z(x, y_l^{<t})$.However, this assumption seems questionable. Even if $y_w$ and $y_l$ are both generated on-policy, since there is randomness during sample and the generated response is long, even some slight variation at the beginning might leads to significantly different prefix $y^{<t}$. Therefore it is not appropriate to make such assumption.
4. The equation right above equation (17) gives a way to distribute sentence level reward to token-level reward. However, such distribution is not well-motivated. In fact, [1] gives the exact reward distribution as $r(s_t,a_t) = \beta \log \pi_{\theta} / \pi_{\text{ref}} + V(s_{t}) - V(s_{t+1})$. Therefore, the reward distribution is valid only when $V(s_{t}) = V(s_{t+1})$, which is not established in the paper.
[1] Rafailov, Rafael, et al. "From $ r $ to $ q^* $: Your language model is secretly a q-function." arXiv preprint arXiv:2404.12358 (2024).
Experimental Designs Or Analyses: Extensive experiments are conducted, and the results looks convincing to me.
Supplementary Material: I briefly went over the proof of theorems. See above for regarding issues.
Relation To Broader Scientific Literature: This paper adapts DPO to token-level reward and the relation with previous works are mostly clearly stated
Essential References Not Discussed: I don't see a missing of significant related works.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1 Clarification regarding Equ. 8**
By [1] (Thanks to Reviewer **aioX**), Equ. (8) has connections to an approximation approach common in prior RL works [2, 3, 4]. [1] pointed out this by providing 5 papers including [2, 3, 4], and followed this line to derive the loss function for their DPO, please see Appendix B.2.1 in [4]. Hence, this is a reasonable approach. We will give citations and provide related illustrations.
Moreover, it was pointed out in [5] that "[6] showed that under the Max-Entropy RL formulation, the token-level log-ratio $\log \frac{\pi_{\theta}(y|x)}{\pi_{\text{ref}}(y|x)}$ can be seen as an implicit token-level reward or advantage function (invariant under reward shaping)."
Notably, our derivation is mainly from the relaxation approach in optimization. Although we start from the state-action reward, the final derived loss function coincides with the streamline of DPO. Specially, when the $\hat{r}(s_t, a_t)$ is not available, we may simply set $\hat{r}(s_t, a_t)=0$ and by Assumption 4.2 our loss function in Equ. (16) is precisely the loss function of DPO, which demonstrates our approach is reasonable.
**Q2 Explanation for $f$ in Assumption 4.2**
Thanks. $f(u)$ is set such that $f(0)=1$ and $|f(u) - 1| \le \varepsilon$. Concrete $f(u)$ can be chosen by users for their personal usage. Please also check our response to **Q8 of Reviewer aioX** to see benefits of introducing $f$.
**Q3 Strong assumption for Equ. 15**
Thank you for the insightful comment!
We have resolved this issue based on the finding that $\delta( f, \hat{r}; x, y_w, y_l)$ does not depend on the policy $\pi_{\theta}$ to be optimized, and the assumptions are removed. The approach is new for canceling partition functions in the BT model.
Now Equ. (15) and its proof have been reorganized as follows:
$$
\Pr(y_w \succ y_l | x) = \sigma\left( \varphi(\pi_{\theta}, f, \hat{r}; x, y_w, y_l) + \delta( f, \hat{r}; x, y_w, y_l) \right), \qquad (1)
$$
where $\delta( f, \hat{r}; x, y_w, y_l)$ does not depend on the policy $\pi_{\theta}$ to be optimized, but only on $f, \hat{r}, x, y_w, y_l$ and the partition function $Z(s_t)$ (does not depend on $\pi_{\theta}$, see Theorem 4.3).
For briefness, let
$$h\triangleq (f, \hat{r}; x, y_w, y_l) .$$
Since $\sigma(t)$ is the sigmoid function with $\sigma'(t)>0$, we have:
**Theorem 1.** The $\Pr(y_w \succ y_l | x)$ in Equ. (1) has the same maximal solution and the same ascent direction as the function $\sigma\left( \varphi(\pi_{\theta}, h)\right)$ with respect to $\pi_{\theta}$.
*Proof.* Note that, $\delta( h)$ is not dependent on the policy $\pi_{\theta}$ and $\sigma'(t)>0$. $d$ is an ascent direction of function (1) if
$$ d^T \nabla_{\pi_{\theta}} \sigma\left( \varphi(\pi_{\theta}, h) + \delta(h) \right) >0,$$
which is equivalent to
$$
\begin{aligned}
& d^T \sigma'\left( \varphi(\pi_{\theta}, h)+ \delta(h)\right) \nabla_{\pi_{\theta}} \varphi(\pi_{\theta}, h) >0 \\
& \Longleftrightarrow d^T \sigma'\left( \varphi(\pi_{\theta}, h)\right) \nabla_{\pi_{\theta}} \varphi(\pi_{\theta}, h) >0 \\
& \Longleftrightarrow d^T \nabla_{\pi_{\theta}} \sigma\left( \varphi(\pi_{\theta}, h)\right) >0.
\end{aligned}
$$
Hence function (1) has the same ascent direction as the function $\sigma\left( \varphi(\pi_{\theta}, h)\right)$.
Similarly,
$$
\begin{aligned}
& \nabla_{\pi_{\theta}} \sigma\left( \varphi(\pi_{\theta}, h) + \delta( h) \right) =0 \\
& \Longleftrightarrow \sigma'\left( \varphi(\pi_{\theta}, h)\right) \nabla_{\pi_{\theta}} \varphi(\pi_{\theta}, h) = 0 \\
& \Longleftrightarrow \nabla_{\pi_{\theta}} \sigma\left( \varphi(\pi_{\theta}, h)\right)
= 0.
\end{aligned}
$$
So Theorem holds.
Thus by Thm 1, since we focus only on optimal $\pi_{\theta}$ of function (1), we may redefine
$$\Pr(y_w \succ y_l | x) \triangleq \sigma\left( \varphi(\pi_{\theta}, f, \hat{r}; x, y_w, y_l)\right), $$
and use it for constructing the loss function in Equ. (16).
We will update the statement and proof of Equ. (15). Thanks!
**Q4 Why $r(s_t,a_t) = \beta \log \pi_{\theta} / \pi_{\text{ref}}$**
It was shown in [6] that $r(s_t,a_t) = \beta \log \pi_{\theta} / \pi_{\text{ref}}$ under the definition of equivalent state-action reward class and invariant re-parameterization, which does not require $V(s_{t}) = V(s_{t+1})$. Please see Theorem 1 there. Moreover, the final loss function in [6] is equivalent to that in [7]. Hence we adopt the equation directly. It is a common practice in many works [5, 8].
[1] A dense reward view on aligning text-to-image diffusion with preference
[2] Approximately optimal approximate reinforcement learning
[3] Relative entropy policy search
[4] Trust Region Policy Optimization
[5] Self-Play Preference Optimization for Language Model Alignment
[6] From r to Q*: Your language model is secretly a Q-function
[7] Direct preference optimization: Your language model is secretly a reward model
[8] Free process rewards without process labels
---
Rebuttal Comment 1.1:
Comment: Thanks for the rebuttal. Some of my remaining concerns are shown as follows
Q1: Thanks for providing the references. However, the question, "the objective in equation (8) is to myopically optimize the reward of the currect step without considering further states but why this objective is applied" is not directly answered.
Q2: Thanks the author for the comment. However, it is still unclear to me how should the user choose the function $f$ according to the personal usage. In A8 to reviewer aioX, the author provide an example to show that certain $f$ can emphasize those token with positive reward. But the motivation behind emphasize that token is still unclear.
Q3: Thanks the author for the updated proof. However, (potentially due to space limit), the revised proof is hard for me to follow. At a high level, the new proof indicates that $\delta(f, \hat{r}; x, y_w, y_l) =0$, which is quite counter-intuitive.
Q4: Thanks for the clarification. My concerns regarding this part are fully addressed.
---
Reply to Comment 1.1.1:
Comment: **A1:** We must clarify that our final derived equation optimizes the reward of the whole trajectory just like DPO. Equ. (8) is only the starting step for the subsequent derivations. Indeed, the ground-truth unknown reward $r_{\phi}(x,y)$ is decomposed into the token level in Equ. (6), and Equ. (8) is for representing the token-level reward $r_{\phi}(s_t, a_t)$ with some policy in the subsequent derivation.
Specifically, from Equ. (13), the current step $r_{\phi}(s_t, a_t) = \beta \log\frac {\pi_{\theta} (a_t|s_t)}{\pi_{\text{ref}}(a_t|s_t)} + \beta \log Z(s_t)$, where the partition function does not depend on $\pi_{\theta}$. Suppose W.L.O.G. the trajectory generation of LLM is in finite time-steps, then the policies of all time-steps in the equation can be re-parameterized into one policy $\pi_{\theta^*}$ such that each log-ratio has the same value as the original one, due to huge number of parameters. Then (for easy presentation, let $f(\cdot)\equiv 1$), it is obvious that:
$$
r_{\phi}(x, y) = \sum_{t=1}^T \left[\beta \log\frac {\pi_{\theta^*} (a_t|s_t)}{\pi_{\text{ref}}(a_t|s_t)}+ \beta \log Z(s_t) \right]
= \beta \log\frac {\pi_{\theta^*} (y|x)}{\pi_{\text{ref}}(y|x)} + \beta \sum_{t=1}^T \log Z(s_t).
$$
Next, with the Bradley-Terry preference model, the per-instance loss $\sigma( \varphi(\pi_{\theta}) + \delta )$ in Equ. (15) is adopted for maximizing to obtain an optimal policy $\pi_{\theta}$. By Theorem 1, $\sigma( \varphi(\pi_{\theta}) + \delta)$ and $\sigma( \varphi(\pi_{\theta}))$ have the same maxima and ascent directions w.r.t. $\pi_{\theta}$, hence we can redefine
$$\Pr(y_w \succ y_l | x) \triangleq \sigma ( \varphi(\pi_{\theta})), $$
and use it to construct the loss function in Equ. (16). In this case, it is exactly the per-instance loss of DPO.
**A2:**
**(1) How to choose $f$:** Our proposed $f$ in Equ. (17) have demonstrated promising performance in RLHF experiments, which is the primary use case for preference optimization algorithms. We believe this makes it a reasonable default choice for similar scenarios. For other use cases, $f$ can be customized accordingly. For example, if smoother guidance is desired, users may use a sigmoid function over $\hat{r}$ in the proposed $f$. Many different choices of $f$ can satisfy Assumption 4.2, and determining the optimal one remains an open problem, promoting further research.
**(2) Motivation of Equ. (17):** Consider the case in **A8 to reviewer aioX**, if $\hat{r}(s_t, a_t)>0$, i.e., the reward is a positive, then the action $a_t$ in state $s_t$ is preferred. This implies that the state-action $(s_t, a_t)$ should be reinforced, and then it is assigned a larger weight $1 + \alpha \hat{r}([x, y_w^{<t}], y_w^t)$. In this way, the gradient of our loss function $\mathcal{L}\_{\text{TGDPO}}(\pi_{\theta})$ at this state-action is
$$
\beta (1 + \alpha \hat{r}([x, y_w^{<t}], y_w^t))\nabla_{\pi_{\theta}}\log\frac {\pi_{\theta} (y_w^t|[x, y_w^{<t}])}{\pi_{\text{ref}}(y_w^t|[x, y_w^{<t}])},
$$
which is scaled up by $1 + \alpha \hat{r}([x, y_w^{<t}], y_w^t)$. As a result, optimizing our loss function encourages the policy to assign higher probability to the action that leads to higher reward in the given state. In contrast, if $\hat{r}(s_t, a_t)<0$, then the action is a dispreferred one, and is progressively assigned lower probability. The other cases are omitted due to limit space. This weight adjustment allows our TGDPO to optimize the policy more effectively, as demonstrated in our experiments.
**A3:** We must clarify that your high level indication $\delta(f, \hat{r}; x, y_w, y_l) =0$ is not correct. For example, suppose $\varphi= -t^2$, $\delta=1$, then $\sigma(\varphi )$ and $\sigma(\varphi + \delta)$ have maximizer $t=0$, but in this case $\delta=1$.
In **A3 to your Q3 in our previous reply**, we have shown the result in a formal way. For easier understanding, let's give it in a compact form.
In the main text, Theorem 4.3 shows that the partition function $Z(s_t)$ and $s_t$ do not depend on $\pi_{\theta}$. Moreover, $\delta(\cdot)$ also does not depend on $\pi_{\theta}$. For your understanding, we simplify in the sequel all notations independent of $\pi_{\theta}$ to be optimized, then the Bradley-Terry preference model in Equ. (15) is $\Pr(y_w \succ y_l | x) = \sigma( \varphi(\pi_{\theta}) + \delta)$, and the Theorem in **A3 to your Q3 in our previous reply** is exactly as:
**Theorem 1.** For the policy $\pi_{\theta}$, the function $\sigma( \varphi(\pi_{\theta}) + \delta)$ has the same maxima and ascent directions as the function $\sigma( \varphi(\pi_{\theta}) )$, here $\sigma(t)$ is the sigmoid function.
Then it is easy to show Theorem 1 is correct since the sigmoid function $\sigma(t)$ is strictly increasing. | Summary: This paper introduces TGDPO, an enhanced version of Direct Preference Optimization (DPO) that incorporates token-level reward guidance to address the limitations of conventional sentence-level DPO. While prior methods like Proximal Policy Optimization (PPO) benefit from fine-grained token-level rewards, DPO, formulated as a sentence-level bandit problem, struggles to leverage such granular signals. To bridge this gap, the authors decompose sentence-level PPO into a sequence of token-level PPO problems, enabling the derivation of a closed-form optimal token-level policy and its corresponding token-level reward. By integrating these token-level rewards with the Bradley-Terry preference model, the proposed TGDPO algorithm introduces a new loss function that guides optimization at the token level.
Experiments on MT-Bench, AlpacaEval 2, and Arena-Hard demonstrate TGDPO’s superiority over standard DPO. The method also experimentally exhibits robustness to variations in token-level rewards and provides control over convergence speed.
Claims And Evidence: Please see the Experiment and Question section.
Methods And Evaluation Criteria: The method is the direct result of the theoretical analysis; please see questions in the Theoretical Claims section.
Theoretical Claims: I have carefully reviewed all the theoretical deductions and proofs, and I have some questions:
1. The modified token-level DPO depends on the choice of $\hat{r}$, which does not seem to be a well-defined problem.
2. In the proof of the Bradley-Terry Model with Token-Level Reward Guidance in Equation 15, the assumption $T_w \approx T_l$ and $Z([x, y_w^{<t}) ~= Z([x, y_l^{<t})$ made by the authors in lines 691-692 is very strong.
However, the data $y_w$ and $y_l$ in the offline dataset used to train the DPO may not be generated from the same model. In practice, we might only have the positive data $y_w$, and we generate $t_l$ through negative sampling, or the pairs
$\{y_w, y_l\}$ could be generated using two different models.
Hence, the assumption that $T_w \approx T_l$ and $Z([x, y_w^{<t}) ~= Z([x, y_l^{<t})$ may not hold in this case.
This could significantly affect the subsequent deductions of the method.
Additionally, the assumption should be mentioned in the main text.
3. In Line 311-313 (left), how can we get this equation? and in practice, should we always need to run DPO first to get the $\hat{r}$.
Experimental Designs Or Analyses: 1. In Tables 1-4, how is the win rate calculated? Why do the scores between the methods appear similar, yet the win rates vary?
2. In Table 2, the number of baselines is relatively small. It would be beneficial to compare against additional baselines, especially TDPO, which is the most closely related work to this paper.
3. Will the choice of $f()$ affect the results? The experiment lack the ablation study of the choice of $f$.
4. In Section 5.3, how is convergence defined? Additionally, how do the authors select checkpoints (no convergence results) in other sections
5. In Tables 2-4, why is the score not reported
6. Are the results stable? It would be better to report the standard deviation.
Supplementary Material: There is no supplementary material.
Relation To Broader Scientific Literature: The method might benefit other important aspects of LLM alignment, such as safety, honesty, and fairness.
Essential References Not Discussed: The literature review on RLHF could benefit from incorporating additional studies on DPO variants.
Other Strengths And Weaknesses: Strengths:
1. This paper is well-written, and the method is well-motivated by rigorous theoretical analysis. The idea is both novel and interesting.
2. The experiments demonstrate the effectiveness of the method, highlighting additional advantages regarding convergence properties. The authors also provide valuable insights from the experiments.
Weaknesses:
Overall, after carefully reading the paper, I believe this paper meets the acceptance criteria. However, I have several questions regarding the theoretical and experimental sections, which prevent me from confidently voting for acceptance. Please refer to the other sections for detailed questions and concerns.
Other Comments Or Suggestions: No.
Questions For Authors: 1. In lines 221-223 (left), why is "the token-level reward only used as guidance, and we do not require it to be very accurate"? Wouldn't an inaccurate token-level reward affect the outcome?
2. Why does $\alpha$ affect the convergence rate? Are there any theoretical insights into this?
3. Do the authors have any plans to release the code?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1 TGDPO's dependence on the choice of $\hat{r}$**
Trained token-level rewards have shown effectiveness for PPO [1, 2]. For DPO, it is interesting to ask if there exists a framework that can incorporate a trained token-level reward explicitly for better performance. Our TGDPO fills this nontrivial gap.
**Q2 Strong assumption for Equ. 15**
Thanks for the insightful comment! Now the assumptions have been removed, the approach is novel. The theorem and proof can be seen in Response to **Q3 of Reviewer F88J**. We will make revisions in the final version.
**Q3 How to get the Equation in Lines 311-313 (left)? How to get $\hat{r}$ in practice?**
Thm 1 of [3] shows
$$r(s_t,a_t) = \beta \log \frac{\pi_{\theta}(a_t|s_t)}{\pi_{\text{ref}} (a_t|s_t)}$$
under equivalent state-action reward class and invariant re-parameterization. The final loss function in [3] is equivalent to that of DPO [4]. So we adopt the result by setting $s_t= [x, y^{<t}]$ and $a_t= y^t$ and get the Equation. This is a common practice in many works [5].
To obtain a token-level reward $\hat{r}$ in practice, we can use off-the-shelf open-sourced models trained by DPO, other methods [1, 2], or run DPO by ourselves.
Thanks. We will illustrate more for this equation in the final version.
**Q4 Clarification on win rate and score**
The win rate is evaluated by calling a judge model (e.g., gpt-4o-2024-11-20) to pairwise compare the responses of the model and a baseline model (e.g., gpt-4-0314) and determine which one is better [6]. The MT-Bench score is evaluated by calling a judge model to directly assign a score to the model's response [7]. Many prior works observed the scores of different methods being similar [6, 8]. This is likely due to the single-instance scoring protocol.
**Q5 Comparison with TDPO**
Below is the experiment result with TDPO under the Llama3-8B-Instruct PairRM setting.
| | Arena-Hard win rate | AlpacaEval 2 win rate | MT-Bench score | MT-Bench win rate |
| - | - | - | - | - |
| SFT | 21.4 |30.6 |7.9 |27.5 |
| DPO |30.4 | 41.7| **8.0**| 37.5|
| TDPO | 30.2 | 40.7|**8.0** | 39.0|
| SimPO |28.7 |39.8 |7.8 | 32.5|
| TGDPO | **34.3**| **43.9**| **8.0**|**41.9** |
Result with TDPO using the SFT model OpenRLHF/Llama-3-8b-sft-mixture is in **Q1 of Reviewer GJSH**. The result table with TDPO under other settings is in this link <https://anonymous.4open.science/r/tgdpo_rebuttal/results_with_tdpo.pdf>
**Q6 Will the choice of $f$ affect the results**
$f(u)$ may be adjusted by parameter $\alpha$ as in Equ. (17). With this, experiment results in Fig. 1 reveal in some degree the effects of different choices of $f(u)$. The outcome benchmark difference presented in Fig. 1 and Tab. 3 is subtle.
Our paper proposes a framework for incorporating existing token-level reward into DPO explicitly, with Equ. (17) as an example. Many choices of $f(u)$ can satisfy Assumption 4.2, which one is the best is left as an open problem for stimulating further research.
**Q7 Clarification on convergence and checkpoint selection**
In Sec. 5.3, we consider loss moving average below a certain threshold (e.g., 0.1) as convergence. In other sections, we train all methods (DPO, SimPO, TGDPO) for 1 epoch and select the checkpoint at the training end.
**Q8 Stability of results**
Below are the Arena-Hard win rate of Llama3-8B-Instruct PairRM and the 95% confidence interval. From the table we can see all methods have similar levels of stability.
| | Arena-Hard win rate | 95% Confidence interval |
| - | - | - |
| DPO | 30.4 | (-2.3, 2.2) |
| SimPO | 28.7 | (-2.0, 2.0) |
| TDPO | 30.2 | (-2.1, 2.4)|
| TGDPO | 34.3 |(-2.3, 2.2) |
**Q9 Would error in token-level reward affect results**
By Assumption 4.2, $|1-f(\hat{r}(s_t, a_t))|\le\varepsilon$ where $\varepsilon$ is small. Moreover, by the choice of $f(\hat{r}(s_t, a_t))$ in Equ. (17), the error can be reduced by the parameter $\alpha$. Thus mild errors in token-level reward may not affect the outcome greatly, as demonstrated in Fig. 1 and Tab. 3.
**Q10 Why does $\alpha$ affect the convergence rate**
Take win response $y_w$ for an example, the other case is similar. In Equ. (16), for $\hat{r}([x, y_w^{<t}], y_w^t)>0$ and larger $\alpha$, the gradient w.r.t. this token is larger, and the convergence would be faster.
**Q11 Code release**
The code will be released upon acceptance.
[1] Preference-grounded token-level guidance for language model fine-tuning
[2] Segmenting text and learning their rewards for improved RLHF in language model
[3] From r to Q*: Your language model is secretly a Q-function
[4] Direct preference optimization: Your language model is secretly a reward model
[5] Free process rewards without process labels
[6] From Crowdsourced Data to High-Quality Benchmarks: Arena-Hard and BenchBuilder Pipeline
[7] Judging LLM-as-a-Judge with MT-Bench and Chatbot Arena
[8] SimPO: Simple Preference Optimization with a Reference-Free Reward | Summary: The paper presents TGDPO, a formulation of direct preference optimization (DPO) with an implicit token-level reward instead of an implicit sentence-level reward, and shows that this novel method outperforms standard DPO and provides interpretable training dynamics
More precisely, the paper makes the following contributions and claims:
1) It derives a token-level RL-finetuning objective that is tractable to optimize (Eq10) and apply DPO to derive a token-level DPO loss.
2) TGDPO outperforms DPO and other variants in popular alignment benchmarks.
3) TGDPO provides satisfactory policies when trained until convergence and is robust to the modified token-level reward pre-training phase.
## update after rebuttal
All my concerns have been addressed. It also seems that the other reviewer's concerns have either been addressed or are not critical. I maintain my score from the end of the rebuttal.
Claims And Evidence: Overall, the claims in the paper are backed by enough evidence, but I have concerns about missing information in the experimental setup.
1) The derivation is backed by theoretical results with clear proofs. See the Theoretical claims for details.
2) Evidence is provided in Table 1, but I have concerns regarding the experimental setup. See the Experimental Designs section,
3) This is well presented in Figure 1 and Tables 2, 3, and 4.
Methods And Evaluation Criteria: I believe that starting from closed-data, fully post-trained models like Llama3-8B-Instruct and Gemma-2-2B-it and then performing further alignment on them gives misleading numbers to the community, as they suggest that the methods presented improve the model further, while what is happening is that they distort their post-training distribution.
The authors do not claim to make the models better than what their original authors did, so this is okay in this paper, but I would strongly recommend the authors to consider only SFT models if possible or add a remark about this.
Otherwise, the choice of evaluation benchmarks and datasets is good. The results would be stronger with an additional dataset, which would be more impactful than varying the reward model, as it only serves for preferences.
Theoretical Claims: I verified the proof of Theorem 4.1. in Appendix A.1.
The theorems to derive the optimal policy and the resulting reward are straightforward modifications of the results in the DPO paper. I did not verify their proofs but believe they hold.
Equation 15 is an important result, but its proof is in the appendix. It would have been nice to provide some intuition in the main paper. I verified the proof. It makes several assumptions, which may or may not hold depending on the data considered. To me, what's important for the paper in this case is that the empirical results still show improvement with this derivation..
Experimental Designs Or Analyses: It's not clear what the starting point of the TGDPO training is. Is it from the already trained DPO model?
TGDPO seems to use double the budget and DPO as it has to train a policy before starting. The authors do not discuss this computational consideration.
It's not clear why SimPO consistently underperforms DPO in Table 1, although the paper uses a similar experimental setup as Meng et al. (2024). This raises concerns regarding the experimental protocol.
Supplementary Material: I reviewed the proofs of the main theorems in the paper.
Relation To Broader Scientific Literature: Sufficient.
Essential References Not Discussed: The authors reference the essential prior work and discuss the differences with the work of Zeng et al. (2024), which is critical to clearly identify the contributions of the paper.
Other Strengths And Weaknesses: Clarity:
-The paragraph in lines 215 column two seems grammatically incorrect. It's not clear what point it conveys.
-I would have appreciated more motivation for the Modified Token-Level PPO problem. Its presentation is a bit abrupt.
+Nevertheless, the interpretation of the loss derived from it with the practical considerations makes up for this lack of earlier motivation. Perhaps its possible to rewrite some parts to connect these two motivations?
Other Comments Or Suggestions: Open to reconsidering my score given input from the authors. My main concern is about missing clarifications for the results and experimental protocol.
Questions For Authors: No additional questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1 Experiment on SFT model**
Thank you for the advice! Below we show the experiment results on UltraFeedback using the open-sourced SFT model OpenRLHF/Llama-3-8b-sft-mixture, which has not been trained by RLHF. Our TGDPO using SimPO's token-level reward achieves much better performance than baselines. Specifically, it achieves win rate gains of 10.5 on AlpacaEval 2 and 3.9 on Arena-Hard compared to best-performing baselines.
| | Arena-Hard win rate | AlpacaEval 2 win rate | MT-Bench score | MT-Bench win rate |
| - | - | - | - | - |
| SFT | 6.2 |5.0 |7.6 |16.3 |
| DPO | 10.2 |9.9 |**7.8** |19.5 |
| TDPO | 11.7 |11.0 |7.5 |15.7 |
| SimPO | 21.4 |16.4 |**7.8** |27.5 |
| TGDPO w/ DPO's token reward | 13.8 |12.8 |7.7 |20.0 |
| TGDPO w/ SimPO's token reward | **25.3** |**26.9** |7.6 |**31.9** |
**Q2 Setting difference between SimPO (Meng et al., 2024) and ours**
The key difference in the experiment setting is that we use the latest and more powerful gpt-4o-2024-11-20 as the judge model, while SimPO uses gpt-4-1106-preview (gpt-4 turbo), which was released in Nov 2023.
Below we compare the Arena-Hard win rate of Llama3-8B-Instruct PairRM using these two judge models. The win rate judged by gpt-4-1106-preview is generally consistent with the SimPO paper, while the result is different from the latest gpt-4o-2024-11-20. This is the reason for SimPO underperforming DPO in Table 1.
| | gpt-4-1106-preview | gpt-4o-2024-11-20 | Avg |
| - | - | - | - |
| DPO | 32.9 |30.4 |31.7 |
| SimPO | 33.5 |28.7 |31.1 |
| TGDPO | 36.9 |34.3 |35.6 |
**Q3 Starting point of TGDPO training**
We would like to clarify that DPO, SimPO, and our proposed TGDPO have the same starting point for training, which are Instruct or SFT models. As described in Equation (16), TGDPO is designed to leverage any token-level reward models, including pre-trained DPO or SimPO models. We can use off-the-shelf open-sourced token-level reward models. So it is not necessary to train a token-level reward model by ourselves before starting TGDPO. Furthermore, TGDPO can enjoy faster convergence speed with satisfactory performances, as demonstrated in Figure 1 and Table 3 of this paper. Also, naively increasing the training budget for DPO or SimPO usually does not improve the performance. As demonstrated in Table 2, training DPO and SimPO to convergence leads to worse performance. We will clarify the description to avoid misunderstanding.
**Q4 Clarification of Equ. 15**
We followed the standard way of conducting experiments and TGDPO consistently outperforms baselines. We believe this empirical validation is a key strength of our approach, as it shows that the theoretical insights lead to practical improvements.
From theory aspect, now the related assumptions have been completely removed, the approach is novel, and the intuition is outlined below:
Let
$$h=( f, \hat{r}; x, y_w, y_l).
$$
The Bradley-Terry model in Equ. (15) is
$$
\Pr(y_w \succ y_l | x) = \sigma\left( \varphi(\pi_{\theta}, h) + \delta(h) \right).
$$
We find that $\delta( h)$ does not depend on the policy $\pi_{\theta}$ to be optimized, but only on $f, \hat{r}, x, y_w, y_l$ and the partition function $Z(s_t)$ (does not depend on $\pi_{\theta}$, see Theorem 4.3 in the main text). Since $\sigma(t)$ is the sigmoid function with $\sigma'(t)>0$, the above $\Pr(y_w \succ y_l | x)$ has the same maximal solution and the same ascent direction as the function $\sigma\left( \varphi(\pi_{\theta},h)\right)$ with respect to $\pi_{\theta}$.
Hence, since we focus only on the maximal solution $\pi_{\theta}$, we may redefine
$$\Pr(y_w \succ y_l | x) \triangleq \sigma\left( \varphi(\pi_{\theta}, h)\right), $$
and use it for constructing the loss function of our preference optimization.
The detail can be seen in response to **Q3 of Reviewer F88J**. We will provide the intuition in the final version.
**Q5 Difference with TDPO (Zeng et al., 2024)**
Our work aims to leverage an existing token-level reward to guide DPO training at the token level. Whereas, TDPO aims to enhance the regulation of KL-divergence by constraining each token with forward KL-divergence. It is not guided by a token-level reward.
We will add more discussions on the differences with TDPO in the final version.
**Q6 Clarification on line 215**
The paragraph demonstrates that it is possible to obtain a token-level reward, using the approach in [1, 2] or DPO. And, the token-level reward will be adopted for shaping the reward in PPO and subsequently the loss function of DPO.
We will make the description better.
[1] Preference-grounded token-level guidance for language model fine-tuning
[2] Segmenting text and learning their rewards for improved RLHF in language model
---
Rebuttal Comment 1.1:
Comment: I thank the authors for addressing my concerns. One concern remains:
> It's not clear why SimPO consistently underperforms DPO in Table 1, although the paper uses a similar experimental setup as Meng et al. (2024).
Edit:
The authors have cleared the above concern by providing evidence of experiments with the same protocol showing SimPO underperforming DPO. It appears that although these papers all use the same model, dataset, and hyperparameters, they do model selection differently, and often do not report how model selection has been done.
I do believe the authors selected the best model for each algorithm with the same criterion, so all my concerns are cleared now. I'm increasing my score from 1 to 4.
---
Reply to Comment 1.1.1:
Comment: We appreciate the reviewer’s continued engagement and would like to clarify the concern regarding the performance gap between SimPO and DPO for Instruct models using the Ultrafeedback dataset in Table 1 of our main paper.
As noted previously, the key difference lies in the evaluation setup. While we strictly followed the official implementations and hyperparameter searches of all baselines, we use the most recent and powerful gpt-4o-2024-11-20 as the LLM judge, whereas the original SimPO paper used gpt-4-1106-preview (gpt-4 turbo), released in November 2023. This distinction is critical, as LLM-based evaluation can be sensitive to model versions: different LLM judges may exhibit different preference distributions due to improvements or shifts in alignment objectives.
To further isolate this factor, we include results in **Q2** using gpt-4-1106-preview, the same judge as in the SimPO paper. Under this setting, SimPO indeed outperforms DPO, consistent with SimPO's observation. However, when evaluated under gpt-4o-2024-11-20, DPO shows better performance. We believe this update in the LLM judge likely contributed to the observed change in relative performance between DPO and SimPO.
Furthermore, similar behavior has been reported in independent studies for Instruct models using the Ultrafeedback dataset. For instance, in [1], which also uses the UltraFeedback dataset (denoted as Zephyr setting), SimPO is shown to underperform DPO across multiple Instruct models when using the UltraFeedback dataset:
- **Table 2 (right column)**: SimPO underperforms DPO on Llama3-8B-Instruct.
- **Table 8 (right column)**: SimPO underperforms DPO on Mistral-7B-Instruct.
- **Table 7**: SimPO underperforms DPO in multi-iteration preference optimization.
Importantly, our experiments in **Q1** show that SimPO outperforms DPO for SFT models, which is consistent with [1]. Our TGDPO also achieves better performance using SimPO's token reward in this case.
Lastly, we emphasize that we treated all baselines fairly and applied consistent settings across all methods. We do not believe the observed performance discrepancy undermines the validity of our experimental protocol or the strength of our contributions since our TGDPO can leverage the token reward from DPO, SimPO, or any other token-level reward models.
**[1] Paria Rashidinejad and Yuandong Tian. Sail into the Headwind: Alignment via Robust Rewards and Dynamic Labels against Reward Hacking, ICLR 2025.** | null | null | null | null | null | null |
TS-RAG: Retrieval-Augmented Generation based Time Series Foundation Models are Stronger Zero-Shot Forecaster | Reject | Summary: This paper proposes TS-RAG, a retrieval-augmented forecasting framework that enhances zero-shot time series prediction by integrating retrieval-augmented generation (RAG) with a pretrained Time Series Foundation Model. The model consists of two key components: a retriever that selects relevant historical time series patterns from a retrieval knowledge base, and a Mixture-of-Experts (MoE) augmentation module that dynamically fuses retrieved sequences with the input query. TS-RAG leverages retrieved information to refine predictions, improving both accuracy and interpretability. The retrieval process is based on embedding similarity, identifying the most relevant sequences from a multi-domain database. The MoE module then adaptively assigns importance weights to retrieved sequences, ensuring effective knowledge integration.
Claims And Evidence: Certain inconsistencies and ambiguities raise concerns about the clarity and validity of some claims in the paper.
C1: The text states that the TSFM encoder is pretrained to generate embeddings, while the figures suggest that the encoder is frozen during inference. This discrepancy affects the understanding of the retrieval process—if the encoder is frozen, it means no further domain adaptation occurs post-pretraining. However, if it is simply pretrained, it implies potential fine-tuning or adaptation.
C2: The paper claims that the augmentation module follows an MoE approach, but the actual implementation does not align with traditional MoE in Transformers or LLMs in my opinion. TS-RAG appears to simply apply a weighted sum over retrieved time series segments, without distinct expert specialization. This misalignment with conventional MoE terminology could be misleading and may require a more precise description.
C3: There is no clear mathematical formulation/ context description demonstrating the presence of self-attention/Transformer backbone mechanisms
Methods And Evaluation Criteria: I have some concerns regarding the suitability of the benchmark datasets used.
The datasets used in the paper, including Weather, ECL, exchage, and ETT, may not be ideal for evaluating long-term time series forecasting. For example, predicting weather for 30 days in advance might not be realistic from a physical standpoint. While these datasets are commonly used in previous methods like Informer, Autoformer, TimesNet, and TimeLLM, the concerns raised in the NeurIPS 2024 conference about the appropriateness of such datasets for long-term forecasting suggest that the relevance of these datasets should be reconsidered [1].
[1] Fundamental limitations of foundational forecasting models: The need for multimodality and rigorous evaluation, https://cbergmeir.com/talks/neurips2024/
Theoretical Claims: The paper does not include formal mathematical proofs or rigorous theoretical claims that would require verification.
Experimental Designs Or Analyses: My concerns are same as 'Methods And Evaluation Criteria' Section.
Supplementary Material: It appears that no supplementary material was provided, which raises concerns about reproducibility and methodological transparency. The lack of open-source code limits the ability of the community to replicate and validate the results. Without access to code or supplementary experiments, it becomes difficult to fully assess the robustness of the approach.
Relation To Broader Scientific Literature: The use of RAG for time series forecasting is a promising and emerging idea. While RAG has been widely explored in NLP, its application in time series forecasting remains relatively underexplored, with only a few recent works attempting to integrate retrieval-based enhancements into temporal modeling.
This paper contributes to this growing area by proposing TS-RAG, which aims to leverage retrieval-augmented learning for zero-shot forecasting. Although there have been some prior studies applying retrieval mechanisms in time series tasks (e.g., ReTime for relational retrieval in spatiotemporal data, or retrieval-based knowledge augmentation for diffusion models in time series), this work extends the idea.
Essential References Not Discussed: [1] Tire K, Taga E O, Ildiz M E, et al. Retrieval Augmented Time Series Forecasting[J]. arXiv preprint arXiv:2411.08249, 2024.
Other Strengths And Weaknesses: For strength, I think that the strength for this paper is:
* **Easy to Read**: The writing is clear and well-structured, and easy to read.
* **Innovative Use of RAG in Time Series Forecasting**: The paper extends RAG to time series forecasting, an underexplored yet promising direction.
* **Zero-Shot Forecasting Focus**: Addresses a critical challenge in time series modeling by improving generalization without fine-tuning, aligning with the trend of foundation models.
For weakness part, please refer to the question part.
Other Comments Or Suggestions: Please refer to the question part.
Questions For Authors: Q1 TO Q3: see **Claims And Evidence**
Q4: The datasets used in the paper, including Weather, ECL, exchage, and ETT, may not be ideal for evaluating long-term time series forecasting. For example, predicting weather for 30 days in advance might not be realistic from a physical standpoint. While these datasets are commonly used in previous methods like Informer, Autoformer, TimesNet, and TimeLLM, the concerns raised in the NeurIPS 2024 conference about the appropriateness of such datasets for long-term forecasting suggest that the relevance of these datasets should be reconsidered [1].
Q5: It appears that no supplementary material was provided, which raises concerns about reproducibility and methodological transparency. The lack of open-source code limits the ability of the community to replicate and validate the results. Without access to code or supplementary experiments, it becomes difficult to fully assess the robustness of the approach.
Q6: Given that identical historical time series can lead to different futures (Time Series Data Phantom Issue), how does TS-RAG ensure that retrieval-based augmentation does not introduce misleading patterns? Additionally, since different types of time series may share similar historical patterns but contain different underlying information, how does TS-RAG prevent incorrect generalization across domains?
Q7: The paper states: "Note that we could select a different TSFM compared to the TSFM encoder in retriever." What are the performances of using the same vs. a different backbone for retrieval and forecasting? Would using the same architecture improve compatibility between the retrieval and forecasting components?
Q8: Does TS-RAG always require a Transformer-based backbone?
If not, what alternative architectures could be used, and how would that affect forecasting performance?
Q9: How are subsets selected from the Chronos pretraining dataset?
How is the retrieval knowledge base subset further extracted?
Q10: How does the embedding method impact retrieval?
Different embedding techniques focus on different aspects of time series (e.g., trends, seasonality, local structure). How does TS-RAG ensure that the chosen embedding method aligns well with its retrieval goals?
Q11: Should embeddings account for absolute timestamps (e.g., 12:00–18:00 vs. 02:00–08:00)? Two sequences might have similar embedding values but occur in completely different time contexts, potentially leading to incorrect retrieval. How does TS-RAG address this?
Q12: The derivation of $\hat{e_q}$ is not explicitly explained.
Q13 The paper lacks formula numbering, which would drop clarity when referencing equations.
Q14 Standard Mixture-of-Experts (MoE) models often require load balancing to ensure different experts contribute meaningfully.
Does TS-RAG implement any mechanism to balance contributions across retrieved time series, or is the fusion process purely weight-based?
Q15: How is the 50M sample selection performed?
Is it ensured that the sampled dataset covers all categories of time series to avoid retrieval bias?
Q16: If the model encounters completely new time series patterns, how does it avoid retrieving irrelevant sequences?
Does TS-RAG include a confidence measure or fallback mechanism for cases where retrieval provides non-useful sequences?
Q17: Real-world time series are not always of fixed length, unlike the fixed-length context windows used in this paper.
How does TS-RAG handle varying-length time series in embedding and retrieval queries?
Q18: Compared to other models, TS-RAG effectively leverages more pre-existing information.
Could this additional prior knowledge be the primary reason for its superior performance, rather than the retrieval mechanism itself?
Q19: The paper states that increasing $K$ improves performance but increases computational cost, but no theoretical or experimental analysis is provided.
Q20: Prior research [2] suggests that introducing noisy or less relevant documents in RAG does not always degrade performance and can sometimes improve it.
What would happen if TS-RAG introduced less relevant retrieved sequences? Would this improve robustness or degrade accuracy?
Q21 What is the proportion of retrieving same-domain time series (e.g., predicting traffic using only traffic data) vs. cross-domain time series (e.g., predicting traffic using electricity demand patterns)?
Does TS-RAG favor in-domain retrieval, or does cross-domain retrieval provide additional generalization benefits?
[1] Fundamental limitations of foundational forecasting models: The need for multimodality and rigorous evaluation, https://cbergmeir.com/talks/neurips2024/
[2] The Power of Noise: Redefining Retrieval for RAG Systems
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Q1:
Thank you for your concern. The TSFM encoder used for retrieval is frozen during both pretraining and inference. It is directly adapted from a pretrained TSFM model on diverse datasets, requiring no further fine-tuning.
Q2:
Thank you for the observation. We agree our augmentation module differs from standard MoE and is better described as a retrieval-based soft MoE [1]. Retrieved horizon representations act as experts, with a gating mechanism assigning soft weights to all top-k segments—unlike traditional MoE, which uses top-1 or top-2 for sparsity. We’ll revise the description accordingly in the updated paper.
Q3: We will add the formulation of the transformer in the updated version.
Q4: We appreciate the reviewer’s concerns and acknowledge the limitations of current benchmark datasets. We use these datasets as they are widely recognized and offer a standardized testbed for fair comparisons. That said, we agree that more realistic, diverse and especially multimodal benchmarks are necessary for better reflecting real-world forecasting challenges.
Q5: The codes can be found here: https://shorturl.at/l1Fv4
Q6: To avoid misleading retrievals, the retriever encoder in TS-RAG is pretrained on a forecasting task using future values as supervision, ensuring that series with similar future dynamics are mapped to similar embeddings. Pretraining on diverse, multi-domain datasets further enables the model to capture various temporal patterns and domain-specific features. The MoE module further helps avoid the negative impact of misleading patterns (See answer to Q2, reviewer 4x4W).
Q7& Q10: Please refer to the response of Q6, and answer to Q4 for reviewer 4x4W
Q8: TS-RAG is not limited to Transformer-based TSFMs; it can be built upon any architecture. The forecasting performance largely depends on the representation quality of the chosen backbone. Since TS-RAG aims to enhance the base model, stronger TSFMs generally yield better results. We also provide a MOMENT-based TS-RAG result in the anonymous repo.
Q9: We randomly sample subset from the full Chronos pretraining dataset. The retrieval knowledge base is then randomly selected from the pretraining subset. Note that for retrieval, we remove sequences with a Euclidean distance of zero.
Q11: We observed that top-k retrieved series often share similar timestamps with the query, suggesting temporal information is encoded in the embeddings. As noted in Q6, similar embeddings imply similar future dynamics. Even with mismatched time contexts, the MoE module adaptively weights and fuses useful patterns to improve forecasting.
Q12: We mentioned in line 202 “the query time series representation eˆq ∈ R 1×d generated by the TSFM"
Q13: We will include the formula numbering in the updated version.
Q14: TS-RAG does not implement a load-balancing mechanism; the fusion process is purely weight-based.
Q15: Refer to Q9
Q16: First, the pretrained retriever encoder helps retrieve series with similar future dynamics (see Q6). Second, we use domain-aligned historical data to reduce irrelevant retrievals. Third, since retrieved horizons may differ from targets, TS-RAG dynamically integrate retrieved contexts for better predictions (see Q11). Finally, we appreciate the suggestion that adding confidence or fallback mechanisms is a valuable future direction.
Q17: Similar to NLP, TS-RAG handles variable-length series using padding to standardize inputs, enabling comparison in a shared embedding space. As a future work, we plan to explore variable-length knowledge bases with adaptive retrieval tailored to each series’ natural length.
Q18: We would like to emphasize that TS-RAG is a general framework designed to enable existing TSFMs to effectively utilize external knowledge. A stronger TSFM backbone naturally contributes to better performance. But the retrieval mechanism also plays a critical role by providing additional gains in accuracy and interpretability.
Q19:With K kept small (≤20), the overhead is minor—e.g., at K = 5/10/15, forward pass takes 0.36/0.44/0.54 ms per query—showing limited impact in practice. A more detailed analysis will be included in the updated paper.
Q20: Thank you for highlighting this paper. While RAG systems in QA are sensitive to noisy documents, the impact of noise in TS-RAG remains unclear. We agree that it's a valuable future direction and will explore it further in subsequent studies.
Q21: Thank you for the thoughtful question. We conducted ablation studies under two settings: (1) distribution shift (e.g., using ETTh1 as knowledge base for ETTh2) and (2) cross-domain retrieval (e.g., using weather data as knowledge base for ETT). The results (https://shorturl.at/JxB7x) show TS-RAG performs best with same-domain retrieval and worst in cross-domain, highlighting the importance of domain alignment.
**We will add the missed reference in the updated version.**
[1] Puigcerver, Joan, et al. "From sparse to soft mixtures of experts."
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Rebuttal Comment 1.1:
Comment: Thank you for the response, which has resolved most of my concerns. Although I still harbor doubts about whether the Weather, ECL, Exchange, and ETT datasets are genuinely suitable for long-horizon forecasting, I acknowledge that this issue extends beyond the scope of this paper. The authors' explanation—that these datasets serve as community-recognized, widely used benchmarks facilitating fair comparison and reproducibility—is acceptable. Accordingly, I have decided to raise my score to 3.
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Reply to Comment 1.1.1:
Comment: We sincerely appreciate the reviewer’s constructive comments and thoughtful feedback. We're glad that our rebuttal helped address your concerns and are grateful for the updated score and support. Your insights have been valuable in improving the clarity and quality of the paper. Thank you again for your time and careful review. | Summary: The authors introduce TS-RAG, a method designed to enhance the performance of a Time-Series Foundation Model (TSFM) by augmenting time-series sequences using an external database. The approach leverages the TSFM’s encoder to embed the input query, retrieve relevant candidate sequences, and weight them using a Mixture of Experts (MOE) module before merging them with the original query for final output generation. Experimental results validate the effectiveness of the proposed method.
## update after rebuttal
Thank you for responding to my questions. For now, I will keep the score as is.
## reviewer's after-rebuttal response ends here
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: Yes.
Supplementary Material: I have reviewed the discussion on models other than Chronos.
Relation To Broader Scientific Literature: There is a growing literature on the RAG systems and Time series foundation models. There is very little work on understanding the applicability of RAG in TIme series foundation models. This paper attempts to apply a RAG framework on TSFMs.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths:
1. TS-RAG effectively utilizes the TSFM’s embeddings to retrieve relevant sequences from an external database, presenting an innovative way to enhance time-series forecasting. The application of MOE is well-motivated and appropriate.
2. The evaluation is conducted on widely used benchmark datasets and state-of-the-art TSFMs, ensuring a rigorous validation of the proposed method.
Weaknesses:
1. The Abstract and Introduction claim that the proposed method enhances interpretability, but this aspect is not revisited or substantiated in the later sections of the paper.
2. The effectiveness of TS-RAG is demonstrated primarily using Chronos. Including results from additional TSFMs would provide a more comprehensive understanding of its generalizability.
Other Comments Or Suggestions: The authors could consider sharing the implementation code via an anonymous link for reproducibility.
Questions For Authors: 1. In the formulation of $e_{final}$, each component of $E_{att}$ corresponds to the forecast horizon, whereas $\hat{e_q}$ represents the input query. Since they correspond to different regimes of the input time series, what is the rationale behind combining them?
2. How is the data split ratio determined for the ETT and Weather datasets?
3. The pre-training database is a subset of the Chronos training data. What is the reasoning behind this choice? Would using a different dataset for augmentation be more beneficial in introducing unseen patterns to the model?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Reproducibility:** Thank you for your suggestion, we are glad to provide code, pretrained models, datasets and knowledge base via the anonymous link: *https://anonymous.4open.science/r/TS-RAG-F4DB*
**W1: TS-RAG enhances interpretability** Thank you for your comment. TS-RAG improves interpretability in two key ways: Compared to traditional TSFMs, which often act as black-box models, TS-RAG introduces a retrieval mechanism that explicitly provides similar historical sequences. This allows users to visually examine the retrieved sequences and understand how the model’s forecast is influenced by past events and patterns. During the retrieval and augmentation process, similarity scores and weights are computed, which can be used to highlight the most relevant historical patterns. This provides users with insight into which particular part of historical data contributes most to the prediction, helping them focus on the most informative patterns. We will provide a more comprehensive description of interpretability and show case studies in the updated version of the paper.
**W2: TS-RAG on other backbone** To better evaluate TS-RAG as a general framework, we also implement TS-RAG using MOMENT as the backbone, which consistently outperforms the original MOMENT. The results are in *https://anonymous.4open.science/r/TS-RAG-F4DB/Rebuttal%20and%20Discussion.md* **TS-RAG on other TSFM backbones**, which provide strong evidence for the effectiveness of the TS-RAG framework.
**Q1 Rationale to combine E_att and e_q^:** Thank you for your question. I'd like to clarify that E_att represents the combined embeddings of the query time series and the retrieved future horizons after being processed by an MHA layer. It contains k + 1 components: one for the query and k for the retrieved sequences. The eq^ is the representation of the input query, in the TSFM forward process without RAG, eq^ is passed through a prediction head to generate the forecast. In our approach, we introduce a projection layer to map the retrieved forecast horizons into the same representation space as eq^, this alignment enables effective fusion of the query representation and the retrieved information, leading to forecasting performance improvements.
**Q2 How to determine data split ratio:** We follow the standard data split convention used in published papers[1,2].
Ref:
[1] Wu, Haixu, et al. "Timesnet: Temporal 2d-variation modeling for general time series analysis." arXiv preprint arXiv:2210.02186 (2022).
[2] Jin, Ming, et al. "Time-llm: Time series forecasting by reprogramming large language models." arXiv preprint arXiv:2310.01728 (2023).
**Q3 Rational choosing subset of the Chronos training data:** The pre-training database is a subset of Chronos’s training data. 1) This is a consideration of the trade-off between model performance and retrieval efficiency. 2) This choice ensures that Chronos-bolt is already familiar with the training data, as we will freeze the parameters of Chronos-bolt and only train the MoE module’s augmentation mechanism. 3) The Chronos’s training data already contains diverse types of time series. Using a different dataset for post-training the TSFM backbone could improve generalization on the targeted specific dataset, but may affect its performance over the original dataset/generalization to other unseen data if the new dataset is not large enough and as diverse as the original dataset. | Summary: This paper proposes TS-RAG, a retrieval-augmented generation based method aimed at improving the generalization ability and interpretability of time series forecasting tasks. This framework does not require task-specific fine-tuning, enabling effective zero-shot forecasting while also providing interpretability for the predictions.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: I have checked the derivation of the formulas.
Experimental Designs Or Analyses: I have checked the experimental setup, the analysis of the experiments, and the ablation studies. All the designs and analyses are reasonable and valid.
Supplementary Material: Yes, both experimental details and showcases.
Relation To Broader Scientific Literature: Many studies have demonstrated that developing foundation models for time series tasks can effectively handle complex temporal dynamics. Therefore, leveraging the semantic information provided by these foundation models is highly valuable for time series tasks.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
The authors explore how to leverage the features extracted by foundation models and the rich information retrieved from dedicated databases, offering a promising solution for time series forecasting tasks. The paper is well-written and supported by a comprehensive set of experiments.
Weakness:
1. Which loss function is used in training? More description is needed to reproduce the results.
2. The authors compared the performance under different foundation models. A comparison with related works should also be provided for reference.
Other Comments Or Suggestions: The contributions can be summarized at the end of the introduction to enhance readability.
Questions For Authors: Based on experience, the top-k samples retrieved from the dataset are crucial for the forecasting of the current time series. In other words, the model’s generalization ability can be attributed to the powerful backbone and the rich retrieval information. How can we know the effectiveness of the Mixture-of-Experts module?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **W1: Training loss and Reproduce** Thank you for your question. TS-RAG uses the same loss as the backbone TSFM during training. Specifically, when using Chronos-bolt as the backbone, we adopt the quantile regression loss used in its original implementation. For full reproducibility, we are glad to provide code, pretrained models, datasets and knowledge base via the link: *https://anonymous.4open.science/r/TS-RAG-F4DB*.
**W2: TS-RAG on other backbone** Thank you for your suggestion. We agree that comparing with related works would provide valuable points. However, to the best of our knowledge, existing related works that combine retrieval-augmented forecasting with zero-shot evaluation do not publicly release their code and models. That said, we have ensured fair comparisons between various TSFMs and TS-RAG with different backbone TSFMs. Our experiments with TS-RAG applied to Chronos-bolt and MOMENT demonstrate that it can significantly improve the performance of the base TSFMs, highlighting the effectiveness of TS-RAG. We will continue to monitor future releases to include such open-source baselines.
**Q1: Effectiveness of the MoE** Thank you for your insightful comment. In the TS-RAG system, the augmentation module is as important as the retriever, as it determines how the retrieved information is integrated into the final prediction. An ineffective fusion mechanism can lead to poor performance. To demonstrate the importance of the Mixture-of-Experts module in TS-RAG, we compare it with a simpler alternative: a gated fusion module that linearly combines the original forecast with the retrieved forecasting horizon (similar to the fusion module in Time-MMD [1]). And we conduct experiments with both augmentation modules under the same pretrain-zeroshot setting. The results in *https://anonymous.4open.science/r/TS-RAG-F4DB/Rebuttal%20and%20Discussion.md* **Effectiveness of Mixture-of-Experts** show that although TS-RAG with a gated fusion module also improves the zero-shot performance, the performance gains are consistently lower than TS-RAG with the MoE module. This provides strong evidence of the effectiveness of the MoE module.
Ref:
[1] Liu, Haoxin, et al. "Time-MMD: Multi-Domain Multimodal Dataset for Time Series Analysis." NeurIPS Datasets and Benchmarks Track (2024). | Summary: This paper presents TS-RAG, a retrieval-augmented-generation-based time series forecasting framework. TS-RAG leverages pre-trained time series encoders to retrieve semantically relevant time series segments from a dedicated knowledge database. Next, it develops a learnable Mixture-of-Experts (MoE)-based augmentation module, which dynamically fuses retrieved time series patterns with the TSFM’s representation of the input query, improving forecasting accuracy without requiring task-specific fine-tuning. This paper evaluates TS-RAG on seven public benchmark datasets, demonstrating that TS-RAG achieves state-of-the-art zero-shot forecasting performance.
## update after rebuttal
I think this paper's main contribution lies in exploring the use of RAG for time series foundation models with some designs and experiments. Some limitations are:
1. How the data in the knowledge base influences the RAG needs further exploration and discussion. When there are in-domain data, this method's relationship with fine-tuning needs to be discussed (such as comparing their performance and efficiency quantitatively, showing their advantages at different aspects). When there are no in-domain data, whether this method still works lacks some rigid guarantees.
2. The designed method is a direct implementation of RAG into time series models, which does not show many novel designs. The improvements are not clear enough on some models, such as Chronos, and the additional cost introduced by RAG is relatively high compared with simple zero-shot inference.
Claims And Evidence: This paper claims that Time Series Foundation Models (TSFMs) lack inherent mechanisms for domain adaptation and are less robust when faced with complex and evolving time series patterns. It is not supported by convincing evidence. It is also unclear by comparing TSFMs with which other models can we get this conclusion.
Methods And Evaluation Criteria: The proposed method does not make sense to me.
1) It seems that TS-RAG highly depends on the high similarity between time series in the knowledge base and the query. How can we guarantee this when performing zero-shot forecasting? Are there any failure cases of this method in situations where no similar knowledge can be retrieved?
2) The retrieval is based on the Euclidean distances between series. Do time series with small Euclidean distances necessarily share similar dynamics or future horizons?
3) It is unclear how to select the encoder for the Retriever. How would this selection affect the performance?
4) It is confusing why we should use subsets to train TS-RAG and serve as the knowledge base since more data may lead to better performance.
Theoretical Claims: There is no proof for theoretical claims.
Experimental Designs Or Analyses: 1) From Table 1, the performance improvement is not significant compared with existing models such as Chronos. Some other SOTA TSFMs are missing, such as Time-MoE [1].
2) It seems that this paper only combines TS-RAG with Chronos and does not show its performance on other TSFM backbones.
3) Table 2 discusses using the historical database. However, in this case, the database and the queries are from the same dataset, which cannot be considered as zero-shot forecasting.
[1] Time-moe: Billion-scale time series foundation models with mixture of experts
Supplementary Material: Yes. I reviewed the appendix of this paper.
Relation To Broader Scientific Literature: This paper tries to improve the performance of existing TSFMs with RAG techniques. The performance improvements are not large compared with TSFMs. The ideas of RAG and MoE in the proposed method are commonly used in time series forecasting or deep learning, and this paper does not make significant changes to these original ideas.
Essential References Not Discussed: There are no essential references not discussed.
Other Strengths And Weaknesses: Other strengths:
1) The proposed method is easy to follow.
2) It is an interesting topic to consider enhancing TSFMs with additional knowledge bases.
Other weaknesses:
1) There needs to be more descriptions on how TS-RAG improves interpretability.
2) It would be better to discuss the training and inference costs of TS-RAG.
Other Comments Or Suggestions: No other comments.
Questions For Authors: Authors are suggested to address the issues or concerns mentioned in the above sections considering claims, methods, and experiments.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Q1: Claims**
We appreciate the reviewer’s concern. While TSFMs are pretrained on diverse datasets and perform well in zero-shot and few-shot settings, they can still struggle with non-stationary data and distribution shifts. Existing TSFMs lack mechanisms to deal with this problem, which motivates our work. TS-RAG addresses this gap by introducing retrieval-based augmentation to enhance adaptability. We will revise the manuscript to clarify this point without overstating the limitations of current TSFMs.
**Q2: How to guarantee high similarity**
Thank you for your question. TS-RAG uses two mechanisms to ensure effective retrieval: 1. building the knowledge base from in-domain data, and 2. using a pretrained retriever encoder that captures future dynamics. Even if no highly similar sequences are included in the knowledge base, the MoE module can adaptively weight and fuse the retrieved patterns, ensuring the performance does not fall below the backbone TSFM.
**Q3: Euclidean distances effectiveness**
Thank you for your comments. To clarify, the Euclidean distance is calculated not in the raw time series space, but in the embedding space generated by a pretrained encoder. During pretraining for the encoder, it's optimized via backpropagation using future values as supervision, so that the embeddings of input sequences are well aligned with their future horizons. As a result, sequences with similar embeddings tend to share similar future dynamics.
**Q4: Encoder choice**
Thank you for your question. The retriever encoder should be pretrained on a forecasting task, while its architecture does not matter. Section 5.3 of [1] also shows that retrieval encoder choice has minimal effect on performance.
**Q5: Subsets for training**
Thank you for your question. The use of subsets for both training and the knowledge base is motivated by a trade-off between the model performance and retrieval efficiency.
**Q6: Significance and Time-MoE**
Thank you for the comments. When applied to another backbone (MOMENT), TS-RAG achieves 11.2% average and 21% max MSE improvement, showing that our method brings consistent and significant gains over different backbones.
We also provide the results of Time-MoE. The tables can be found in the anonymous library https://shorturl.at/JxB7x.
**Q7: Other backbones**
Please refer to answer to **Q6**
**Q8: Zero-shot setting**
Thank you for your comments. We understand the concern for the zero-shot setting and would like to clarify this. The models used for embedding and forecasting are not trained on the target dataset. Our model is pretrained on a different dataset and directly applied to the new domain without additional fine-tuning. This aligns with the classical definition of zero-shot learning in literature [2,3,4].
**Q9: Interpretability**
Thank you for your comment. TS-RAG improves interpretability in two key ways:
1. Compared to traditional TSFMs, which often act as black-box models, TS-RAG introduces a retrieval mechanism that explicitly provides similar historical sequences. This allows users to visually examine the retrieved sequences and understand how the model’s forecast is influenced by past events and patterns.
2. During the retrieval and augmentation process, similarity scores and weights are computed, which can be used to highlight the most relevant historical patterns. This provides users with insight into which particular part of historical data contributes most to the prediction, helping them to focus on the most informative patterns.
**Q10: Training and inference costs**
Thank you for your suggestion.
1. Training: TS-RAG maintains efficiency by freezing the TSFM backbone and only training additional parameters. Preprocessing and caching retrieval indices further optimize training, taking approximately 1 hour on a single NVIDIA A6000 GPU with Chronos-bolt.
2. Inference: During inference, the additional cost mainly comes from the retrieval. TS-RAG uses Faiss for vector similarity search. It retrieves the top-k most similar sequences from the knowledge base. On the ETTh1 dataset, the retrieval process adds 9.2 ms of latency per query, the forward process adds another 0.44 ms. In total, the inference takes 9.62 ms per query, which remains practical for real-time applications.
[1] Liu, Jingwei, et al. "Retrieval-augmented diffusion models for time series forecasting." Advances in Neural Information Processing Systems 37 (2024): 2766-2786.
[2] Xian, Yongqin, et al. "Zero-shot learning — A comprehensive evaluation of the good, the bad and the ugly." Proceedings of the IEEE Conference on Computer Vision and Pattern Recognition (CVPR). 2018.
[3] Brown, Tom, et al. "Language models are few-shot learners." Advances in Neural Information Processing Systems 33 (2020): 1877–1901.
[4] Das, Abhimanyu, et al. "A Decoder-Only Foundation Model for Time-Series Forecasting." arXiv preprint arXiv:2310.10688 (2023).
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Rebuttal Comment 1.1:
Comment: Thank the authors for the rebuttal, which addresses some of my concerns. However, there are some remaining ones:
1. About in-domain data: One advantage of the TSFMs is their zero-shot capability, which handles out-of-distribution or new domains without enough data. The need for in-domain data limits model capabilities in such scenarios. Furthermore, if there exist in-domain data, training a new model or fine-tuning the TSFMs may be more straightforward solutions.
2. About the pretrained encoder: It is not convincing to claim that the choice of the encoder does not make a difference since models pretrained with different architectures and pretraining data may have different performance, which will influence their measurement of data similarities.
3. It remains unclear how the subset size controls the trade-off between the model performance and retrieval efficiency, e.g., what are the performance and efficiency when we choose different subset sizes?
4. It seems that the original MOMENT model does not use zero-shot inference in long-horizon forecasting, and thus, using TS-RAG on this model may not be convincing.
5. During inference, it seems that the latency caused by retrieval is relatively high compared with the forward process.
---
Reply to Comment 1.1.1:
Comment: **We sincerely thank the reviewer for the continued engagement and thoughtful feedback. We're pleased that our previous response helped address your concerns, and we appreciate the opportunity to further clarify the remaining details.**
**1. About in-domain data and fine-tuning**
Thank you for the comment.
(1) **Effectiveness without in-domain data:** We would like to clarify that TS-RAG is still effective even without in-domain data. But if in-domain data is available, the performance of TS-RAG can be further improved. Specifically, the experiments¹ show that TS-RAG can still provide meaningful improvements without in-domain data. Furthermore, the results in Table 2 of our paper confirm that TS-RAG remains effective when using a pre-prepared multi-domain knowledge base (without access to the in-domain data).
¹ *We evaluated two additional retrieval settings—distribution shift (e.g., using ETTh1 as the knowledge base for ETTh2) and cross-domain (e.g., using weather data as the knowledge base for ETT). As shown in https://shorturl.at/JxB7x **Table 4**, TS-RAG consistently improves performance across all retrieval settings.*
(2). **Efficiency:** We focus on zero-shot forecasting. Unlike fine-tuning or training new TSFMs which need to tune the model parameters for the target domain, TS-RAG **does not** require model parameter tuning when deployed to a new domain, making it significantly more efficient in terms of time and computational cost.
(3). **Flexibility:** TS-RAG allows rapid adaptation to changing distributions by simply updating the knowledge base offline, which supports practical and flexible use in real-world scenarios.
**2. About the pretrained encoder**
Thank you for the follow-up question. To support this claim, we conducted additional experiments using pretrained encoders from two other TSFMs, i.e., TTM and MOMENT, as the retriever encoder for comparison.
TTM uses an MLP-Mixer-like architecture, MOMENT is based on a Transformer encoder. The original retriever encoder in our paper is based on Chronos, which is built on a T5 architecture.
We compared the three encoders under the same setup. As shown in https://shorturl.at/JxB7x **Table 2**, the performance based on all three encoders is comparable, and none of them consistently outperforms the others. This supports our earlier response (Q4), i.e., the choice of encoder architecture (among existing TSFMs) has minor impact on performance.
**3. Effect of subset size**
Thank you for raising this question. We would like to clarify this from two perspectives:
**(1). Subset size of the training set:**
We conducted experiments with different subset sizes of the pretraining data. As stated in the paper, we constructed a pretraining corpus of 26 million input-output pairs, randomly sampled from the Chronos pretraining dataset. To investigate the effect of data scale, we trained our TS-RAG model on varying proportions of this data—from 0.1% to 50%.
As shown in https://shorturl.at/JxB7x **Table 3**, the performance of TS-RAG improves as the size of the pre-training dataset grows, but the gains diminish with scale. Specifically, the average MSE (aggregated across 7 datasets used in the paper) improves quickly from 0.1% to 10% of the data, while further improvements from 10% to 50% become minimal.
**(2). Domain relevance matters more than size of knowledge base**
**Table 2** in our paper compares retrieval from a large pretraining database (~2.8 million pairs) with much smaller in-domain databases (e.g., ~8 thousand pairs for each sample in ETTh1). Despite its much smaller size, the in-domain database performs better, highlighting the importance of domain relevance. However, a multi-domain knowledge base remains effective when in-domain data is unavailable.
**4. Zero-shot ability of MOMENT model**
Thank you for the question. The original MOMENT model does not support zero-shot long-term forecasting due to the lack of a pretrained prediction head. We address this by pretraining a prediction head on the same pretraining data used for TS-RAG. As shown in Table 1 of our paper, MOMENT achieves comparable zero-shot performance to other TSFMs, making the use of MOMENT in TS-RAG both fair and reasonable.
**5. Inference latency**
Thank you for the comment. Although retrieval introduces most of the inference latency, we believe the trade-off is rational, as the retrieval-augmented mechanism provides significant improvement in zero-shot performance and improves interpretability.
More importantly, the overall latency remains at the millisecond level per query, which is acceptable even for real-time applications.
Finally, the retrieval-augmented forecasting remains relatively underexplored. Our work is a proof-of-concept, focusing on demonstrating the effectiveness rather than optimizing the efficiency. Our future work will explore optimizations such as GPU acceleration, hashing-based indexing to further reduce retrieval latency. | null | null | null | null | null | null |
ROS: A GNN-based Relax-Optimize-and-Sample Framework for Max-$k$-Cut Problems | Accept (poster) | Summary: This paper proposes ROS, a GNN-based L2O method, to obtain high-quality max-$k$-cut solutions. The one-hot encoding of each node is relaxed to continuous variables, a GNN is used to do node classification task, i.e., assigning nodes into $k$ partitions, and the continuous output from GNN is then used to construct a feasible solution by a random sampling step. Theoretical result guarantees the existence of feasible max-$k$-cut solution when a globally optimal continuous solution is found. Numerical results on various benchmarks show that ROS can indeed provide high-quality solutions in an efficient way.
## update after rebuttal
My concerns are resolved by those extra experimental results and clarifications. A revised version with those details is acceptable.
Claims And Evidence: Claim 1 [the consistency of function values between continuous solution and its mapped counterpart]: theoretically supported in Theorem 3.2, but lack of empirical evidence. The reason is that Theorem 3.2 requires a global optimum for the relaxation, which is practically learned by a GNN. It will be more convincing if the authors could show the difference between objective values of continuous solutions and their integer counterparts.
Claim 2 [ROS can efficiently scale to large instances]: supported in Section 4.
Claim 3 [ROS exhibits strong generalization capabilities]: supported in Section 4.
Methods And Evaluation Criteria: The overall idea of ROS makes sense to me. My only question is about the initial node embeddings. Random embeddings seem to be quite casual and make random seed affect both the training and evaluation. Is it more reasonable to use more meaningful embeddings, e.g., including some neighborhood information?
Theoretical Claims: I roughly checked all proofs and they look correct.
Experimental Designs Or Analyses: I have several concerns about the experiments.
- The extra cost of preparing training dataset is important to evaluate the effectiveness of a L2O method, which is missing in the paper.
- The experiments only test $k=2,3$, making it unclear if ROS could be applied for larger $k$.
- For the weighted benchmark, the edge weights are constrained to $\pm 1$ with 10\% perturbations. Are there any reasons for choosing such specific settiing? Especially observing that ROS achieves the best performance on this setting compared to other methods.
Supplementary Material: I reviewed all supplementary materials.
Relation To Broader Scientific Literature: ROS follows a standard GNN-based L2O setting. The idea of solving relaxation and then retrieving an integer solution nearby is commonly used in integer programming. The random sampling step as shown in Algorithm 1 is already in the literature, e.g., see https://arxiv.org/pdf/2404.17452.
Essential References Not Discussed: The discussion about max-$k$-cut is quite sufficient. But the discussion about the idea of relax-optimize-and-sample in other fields is missing.
Other Strengths And Weaknesses: **Strengths**
- The paper is well-written and easy to follow.
- Theoretical results are solid.
- Simple setting results in good performance over various scenarios.
**Weaknesses**
I already stated most concerns in above. Additionally, the experimental results are unable to show that ROS could generate better solutions compared to other methods except for faster computational time. The word "high-quality" is quite vague. Intuitively, when the objective value of one solution is approaching to the global optimum, it is much harder to further improve it. It is unclear if ROS already gives meaningful or useful solutions to any practical problems.
Other Comments Or Suggestions: - In lines 197-199, after executing Algorithm 1 T times, should one choose the solution with the hightest objective value? if the objective is still defined as Eq. (1).
- The order of references in second column of lines 201-202.
Questions For Authors: I already asked all questions in previous sections. They are majorly about clarifications of experiments for better evaluation the importance of ROS, and how well the theoretical contribution is aligned in practice.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Claims And Evidence
**Response to C1:** Theorem 3.2 requires a global optimum, which is why we introduce Theorem 3.3. It theoretically establishes the expected equivalence between relaxed and integer solutions for all feasible points, not just the global optimum. Our sampling algorithm and experiments rely on Theorem 3.3, ensuring practical relevance. Moreover, to stress your concern, we add one row for the continuous objective function in Tables 10 and 12 in the ablation study (updated in Tables 1 and 2 in [anonymous link](https://anonymous.4open.science/r/Tables_For_cFx5-357C/)), explicitly comparing the continuous objcetive values and their integer counterparts.
## Methods And Evaluation Criteria
**Response to M1:** See "Response to Q1" for Reviewer zJRf.
## Experimental Designs Or Analyses
**Response to E1:** Since ROS is unsupervised, we only generate graphs, not ground truth. As stated in Section 4.1, the training dataset consists of 500 regular graphs, which can be generated within 1 second. The pre-training process runs for only one epoch, requiring just 8.75 seconds in total in our device. In contrast, other L2O baselines, such as ECO-DQN and ANYCSP, demand significantly longer training times, ranging from several hours to multiple days. This highlights the efficiency of ROS in both dataset preparation and model training.
**Response to E2:** We evaluate ROS for larger $k$ (specifically, $k=10$) in our experiments on the real-world Bitcoin-OTC dataset. The corresponding results are provided in Table 1 in "Response to R1" for Reviewer bfPu.
**Response to E3:** We selected the [0.9, 1.1] perturbation range to highlight that ANYCSP struggles even with minimal weight variations, while ROS remains robust across different weight settings in the Max-$k$-Cut problem. To further address your concern, we conduct additional experiments with larger perturbation scales ([0,10] and [0,100]) on the weighted Gset benchmark. The results in Tables 3–6 in [anonymous link](https://anonymous.4open.science/r/Tables_For_cFx5-357C/) show that:
- ROS consistently achieves the best performance in terms of both solution quality and computational efficiency.
- Even under extreme perturbations, ROS maintains its advantage over baselines, demonstrating its robustness in handling arbitrary edge weights.
## Relation To Broader Scientific Literature and Essential References Not Discussed
While [1] also derives relaxation-based approaches and sampling methods on discrete Bayesian optimization, our sampling step is theoretically derived rather than borrowed directly from prior work. Theorem 3.2 establishes the relationship between continuous and discrete solutions at global optimal, which leads to our sampling strategy designing and analysis: each feasible continuous solution defines a categorical distribution over discrete assignments, and sampling from it preserves the expected objective value (Theorem 3.3). This makes relaxation and sampling inherently connected rather than an arbitrary choice. We acknowledge similar ideas in other fields and will expand the discussion in our paper.
## Weakness
As shown in Table 3 of the manuscript and Tables 3–6 in [anonymous link](https://anonymous.4open.science/r/Tables_For_cFx5-357C/), ROS consistently produces the highest-quality solutions while maintaining the fastest computational time in the weighted experiments. Additionally, results on the real-world Bitcoin-OTC dataset (Table 1, response to Reviewer bfPu) demonstrate that ROS effectively handles practical problems, confirming its applicability on weighted Max-$k$-Cut beyond synthetic benchmarks.
## Other Comments Or Suggestions
**Response to C1:** We clarify that the correct selection criterion is to choose the solution with the lowest objective value of $f(X)$, as defined in Problem $(P)$ (right column in Line 131), where $f(X)=Tr(XWX^T)$. This corresponds to the highest objective value of the original optimization problem in Equation (1) due to a constant shift and sign inversion. We will revise the manuscript to explicitly state this selection criterion to avoid confusion.
**Response to C2:** We will replace the order of two literatures.
## Questions for Authors
- We have added extensive experiments, including tests on real-world weighted Max-$k$-Cut instances and perturbation studies across different ranges. These results, detailed in Table 1 in response to Reviewer bfPu and Tables 3–6 (anonymous link), further highlight the importance of ROS.
- Regarding the theoretical contribution, ROS is not a direct adaptation from other fields; its components are tightly integrated. The relaxation and sampling steps ensure consistency between the relaxed and discrete solutions, while the powerful GNN effectively bridges the optimization gap. This demonstrates a strong alignment between theory and practical performance.
## Reference
[1] Michael R, et al. A Continuous Relaxation for Discrete Bayesian Optimization[J].
---
Rebuttal Comment 1.1:
Comment: Thanks for your response. Those extra experimental results and clarifications resolve most of my concerns. I will raise my rating to 3 and suggest the authors add those results properly in a revised version.
---
Reply to Comment 1.1.1:
Comment: > **Comment:** Thanks for your response. Those extra experimental results and clarifications resolve most of my concerns. I will raise my rating to 3 and suggest the authors add those results properly in a revised version.
**Reply:** We appreciate your efforts in reviewing our paper and rebuttal. Thank you for your feedback and for raising the rating. We will incorporate the additional experimental results and clarifications into the revised version to further strengthen the paper. Thank you again for your constructive comments! | Summary: The paper introduces, a GNN-based framework for solving the Max-k-Cut problem by relaxing the discrete optimization problem into a continuous optimization task. A Graph Neural Network (GNN) optimizes the relaxed problem, followed by a sampling-based algorithm to obtain a discrete solution. The authors integrate geometric landscape analysis with statistical theory to establish the consistency of function values between the continuous solution and its mapped discrete counterpart.
Claims And Evidence: Authors show the superiority of their algorithms but it is not clear if baselines involving learning base techniques also used the pretraining and finetuning phase or not.
In addition, some direct baselines have neither been cited nor compared with.
Methods And Evaluation Criteria: - **Baselines:** It appears [1][2] and [3] are related and potential baselines, by suitably changing the loss/reward function. [1], in particular, does not even need the optimization function to be differentiable. Why are they not discussed and compared with?
[1] Rishi Rajesh Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya and Sayan Ranu, "NeuroCut: A Neural Approach for Robust Graph Partitioning", in KDD, 2024.
[2] Anton Tsitsulin, John Palowitch, Bryan Perozzi, and Emmanuel Müller. 2023. Graph clustering with graph neural networks. Journal of Machine Learning Research 24, 127 (2023), 1–21.
[3] Aritra Bhowmick, Mert Kosan, Zexi Huang, Ambuj Singh, and Sourav Medya. 2024. DGCLUSTER: A Neural Framework for Attributed Graph Clustering via Modularity Maximization. In Proceedings of the AAAI Conference on Artificial Intelligence, Vol. 38. 11069–11077.
- **Datasets:** None of the datasets are real. Please include real world datasets containing atleast few thousands of nodes (See [1] for example)
- **Generalizability to $k$:** It appears that the method needs to know the number of partitions ($k$) before inference. Specifically, it needs to train for each specific value of $k$ since it does not generalize to unseen $k$ at inference time. This is evident from line 232 where the output embedding is $\mathbb{R}^{k\times N}$.
Theoretical Claims: Seems intuitively correct but did not go through deeply.
Experimental Designs Or Analyses: - Could you please clarify whether Fig. 2 represents the training time or inference time. Could you please demonstrate scalability with respect to ground-truth generation, training time and inference time explicitly and compare with non-neural approaches. Non-neural approaches generalize to any value of $k$. Hence, it is important to look at the scalability of all three dimensions to evaluate the practical value of this work.
Supplementary Material: Gone through the Ablation study experiments and they seem fine to me.
Relation To Broader Scientific Literature: Earlier works try to solve maximum-k-cut problems using graph learning approaches but they seem limited to the unweighted setting while the proposed approach deals with solving weighted maximum-k-cut problems using GNN.
Essential References Not Discussed: As mentioned above, important related works have not been disucussed and compared to.
[1] Rishi Rajesh Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya and Sayan Ranu, "NeuroCut: A Neural Approach for Robust Graph Partitioning", in KDD, 2024.
[2] Anton Tsitsulin, John Palowitch, Bryan Perozzi, and Emmanuel Müller. 2023. Graph clustering with graph neural networks. Journal of Machine Learning Research 24, 127 (2023), 1–21.
[3] Aritra Bhowmick, Mert Kosan, Zexi Huang, Ambuj Singh, and Sourav Medya. 2024. DGCLUSTER: A Neural Framework for Attributed Graph Clustering via Modularity Maximization. In Proceedings of the AAAI Conference on Artificial Intelligence, Vol. 38. 11069–11077.
Other Strengths And Weaknesses: **Strengths:**
- The paper presents a GNN-based framework for solving the weighted Max-k-Cut problem, converting a discrete optimization task into a continuous one for easier processing, which is interesting and novel
- Compared to the baselines, the results look good both in efficiency and quality.
**Weakness:**
- The authors have not mentioned if leaning-based baselines are used pertaining and fine-tuning steps separately or not.
- Figure 2 appears to be inference time. Please report time for pre-training, training/fine-tuning, etc.
- The method does not generalize to unseen $k$. This appears to be a serious limitation.
- The benchmark datasets do not include any real-world dataset
- Important works have not been discussed and compared to.
- Code base is not shared and hence reproducibility is hampered.
Other Comments Or Suggestions: In Tables 2,3, and 4, you can directly put ROS without finetuning results. It will enhance readability.
Questions For Authors: The key reasons for my current rating are below. I would be happy to revisit the rating if the questions raised below are satisfactorily addressed.
1Justify why the inability to generalize to unseen $k$ during inference is not a severe limitation.
2. Please discuss (and compare with unless there are obvious reasons not to) the missing baselines discussed above.
3. Include real world datasets.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Claims And Evidence
**Response to C1:** Please refer to "Response to W2" for Reviewer bfPu.
## Methods And Evaluation Criteria
**Response to M1:**
- NeuroCUT [1] is a reinforcement learning-based partitioning method, while DGCLUSTER [2] and DMoN [3] employ graph neural networks to optimize clustering objectives. However, these methods are designed for graph clustering, which aims to minimize inter-cluster connections, whereas Max-$k$-Cut seeks to maximize inter-partition connections. As a result, they are not directly applicable to our problem. Additionally, while NeuroCUT claims to support arbitrary objective functions, its node selection heuristics are only tailored for graph clustering, **making it unsuitable for Max-$k$-Cut**.
- Despite these differences, we evaluated NeuroCUT as a representative baseline of graph clustering. We trained it on 500 3-regular graphs as ROS and tested it on Bitcoin-OTC, a real-world signed network with 5,881 nodes and 35,592 weighted edges (ranging from -10 to 10), which captures trust relationships among Bitcoin traders. **The results is shown in "Response to R1" for Reviewer bfPu**, ROS significantly outperforms NeuroCUT and other baselines, further demonstrating its effectiveness for Max-$k$-Cut.
**Response to M2:** We include a real-world dataset, Bitcoin-OTC, in our evaluation, which contains 5,881 nodes and 35,592 weighted edges. The comparison results with baselines on this dataset are presented in "Response to R1" for Reviewer bfPu.
**Response to M3:** Please refer to the "response to W1" of reviewer bfPu for details regarding the generalizability of our method to unseen $k$.
## Experimental Designs Or Analysis:
Figure 2 represents the fine-tuning time for ROS. ROS does not require ground-truth generation, unlike supervised methods. Pre-training for a specific $k$ is lightweight—training on 500 regular graphs for one epoch takes only 8.75 seconds, whereas L2O baselines like ECO-DQN and ANYCSP require hours or even days. The scalability of fine-tuning (inference) time is detailed in Table 1 of the manuscript, and ROS efficiently scales to instances of large $N$.
## Essential References Not Discussed
Please see the response to M1.
## Weakness
**Response to W1:** Please see "Response to W2" for Reviewer bfPu.
**Response to W2:** As stated in Section 4.1, the training dataset consists of 500 regular graphs, and the pre-training process runs for only one epoch, requiring just 8.75 seconds in total. In contrast, L2O baselines like ECO-DQN and ANYCSP require significantly longer training times, ranging from several hours to multiple days. This highlights the efficiency of ROS. The fine-tuning (inference) time is already reported in Section 4.
**Response to W3:** Please refer to the "response to W1" for reviewer bfPu regarding the generalizability of our method to unseen $k$.
**Response to W4:** Please see Response to M2.
**Response to W5:** Please see Response to M1.
**Response to W6:** We upload our code in https://anonymous.4open.science/r/ROS_anonymous-1C88/.
## Other Comments Or Suggestions
Since fine-tuning directly solves test instances, we cannot remove this stage. However, to enhance readability, we now include results for ROS-vanilla (i.e., ROS without pre-training). The updated tables explicitly present ROS-vanilla results, improving clarity. Below are the updated rows in Tables 1, 2, and 3 of the manuscript (Tables 4 and 5 already included ROS-vanilla results):
**Updated Row in Table 1 in manuscripts**
| Model| $N=100, k=2$| $N=100, k=3$| $N=1000, k=2$| $N=1000, k=3$| $N=10000, k=2$| $N=10000, k=3$ |
| - | - | - | - | - | - | - |
| ROS-vanilla | $132.00\pm 1.89$ | $243.75\pm 2.00$ | $1322.95\pm 6.57$ | $2440.55\pm 4.97$ | $13191.25\pm 20.73$ | $24317.40\pm 21.36$ |
**Updated Row in Table 2 in manuscripts**
| Model| G70 ($k=2$) | G70 ($k=3$) | G72 ($k=2$) | G72 ($k=3$) | G77 ($k=2$) | G77 ($k=3$) | G81 ($k=2$) | G81 ($k=3$) |
| - | - | - | - | - | - | - | - | - |
| ROS-vanilla | 9004| 9982| 6066| 7210| 8678 | 10191| 12260| 14418|
**Updated Row in Table 3 in manuscripts**
| Model| G70 ($k=2$) | G70 ($k=3$) | G72 ($k=2$) | G72 ($k=3$) | G77 ($k=2$) | G77 ($k=3$) | G81 ($k=2$) | G81 ($k=3$) |
| - | - | - | - | - | - | - | - | - |
| ROS-vanilla | 8989.38| 9973.75| 6140.50| 7207.13| 8744.47| 10190.37| 12278.70| 14341.25|
## Questions For Authors
**Response to Q1:** Please refer to the "response to W1" for reviewer bfPu.
**Response to Q2:** Please see Response to M1.
**Response to Q3:** Please see Response to M2.
## Reference
[1] Rishi Rajesh Shah et al., NeuroCut: A Neural Approach for Robust Graph Partitioning, in KDD.
[2] Anton Tsitsulin et al., Graph clustering with graph neural networks. In JMLR.
[3] Aritra Bhowmick et al, DGCLUSTER: A Neural Framework for Attributed Graph Clustering via Modularity Maximization. In AAAI.
---
Rebuttal Comment 1.1:
Comment: The generalization to unseen $k$ seems like a hack. I am happy with the other changes made and will increase the rating to 3.
---
Reply to Comment 1.1.1:
Comment: > **Comment:** The generalization to unseen $k$ seems like a hack. I am happy with the other changes made and will increase the rating to 3.
**Response:** We appreciate your efforts in reviewing our paper and rebuttal. We also thank you for your feedback and consideration in raising the rating. Regarding the generalization to unseen $k$, we provide two approaches based on the "pre-training + fine-tuning" framework of ROS:
- **ROS-vanilla**: This method is directly fine-tuned on the test instance without pre-training, avoiding dependency on predefined last-layer dimensions.
- **ROS-partial**: To apply the pre-training technique and improve efficiency while still generalizing to unseen $k$, this variant is pre-trained on $k=2$ while saving all parameters except the last layer. Before fine-tuning, the pre-trained parameters are loaded, and the last layer is randomly initialized to accommodate the new $k$.
As shown in Table 2 in response to Reviewer bfPu, both approaches demonstrate the **flexibility and extensibility** of our "pre-train + fine-tune" framework of ROS. Furthermore, while our framework supports generalization to unseen $k$, we acknowledge that exploring this aspect through model architecture design, as in [1], is an exciting direction. We appreciate your valuable comments once again.
[1] NeuroCUT: A Neural Approach for Robust Graph Partitioning Rishi Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya, Sayan Ranu KDD Knowledge Discovery and Data Mining(KDD), 2024. | Summary: This paper introduces ROS, a GNN-based framework for Max-k-Cut. The authors propose a solution that relaxes the problem to a continuous space, optimizes it with a neural network, and samples a discrete solution. They compare with existing neural and non neural baselines and show they are better in terms of quality and running time.
Claims And Evidence: 1. ROS has better quality . Supported by evaluation on diverse dataset and values of k.
2. Better running time. supported by running time plots.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Did not check proofs in details.
Experimental Designs Or Analyses: Mostly it is clear. Only thing that is not clear whether baselines were fine-tuned?
Supplementary Material: Table 11. Sampling results.
Relation To Broader Scientific Literature: 1. Proposed method does not require any ground truth.
2. Framework uses relaxation approach, which is effective in this setup.
Essential References Not Discussed: [A] NeuroCUT: A Neural Approach for Robust Graph Partitioning
Rishi Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya, Sayan Ranu
KDD Knowledge Discovery and Data Mining(KDD), 2024
[A] solves graph partitoning problem for arbitrary partitoning objectives. The approach is inductive to number of partitioing.
Other Strengths And Weaknesses: Weakness:
1. Kindly clarify if model can do inference on unseen k(number of partitions). Can the model be fine-tuned to different k? If yes, how?
From line 233 it seems output layer is fixed to k.
2. Were the neural baselines also fine-tuned? Kindly clarify.
3. Code is not shared.
Other Comments Or Suggestions: None
Questions For Authors: Check weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## Essential Reference Not Discussed
**Response to R1:**
- NeuroCUT [1] is a reinforcement learning-based partitioning method designed for graph clustering, which aims to minimize inter-cluster connections, whereas Max-$k$-Cut seeks to maximize inter-partition connections. Additionally, while NeuroCUT claims to support arbitrary objective functions, its node selection heuristics are specifically tailored for graph clustering. Due to this fundamental difference, NeuroCUT is not directly applicable to our problem.
- Despite these differences, we compared our methods with NeuroCUT. We trained NeuroCUT on 500 3-regular graphs as ROS and tested it on Bitcoin-OTC [2], a real-world signed network with 5,881 nodes and 35,592 weighted edges (ranging from -10 to 10), which captures trust relationships among Bitcoin traders. As shown in Table 1, ROS significantly outperforms NeuroCUT and other baselines, further demonstrating its effectiveness for Max-$k$-Cut.
**Table 1: Evaluation results on Bitcoin-OTC Datasets.**
| Model | Value ($k=2$) | Time (s) ($k=2$) | Value ($k=3$) | Time (s) ($k=3$) | Value ($k=10$) | Time (s) ($k=10$) |
| - | - | - | - | - | - | - |
| NeuroCut |1424|239.46| 1667| 242.65| 13235| 250.90|
| PIGNN| 14587| 62.31| -| -| -| -|
| MD| 14989| 37.15| 18448| 50.40| 21182| 105.92|
| ANYCSP| 10678| 180.20| 14319| 180.16| 19359|180.24|
| ROS| **15384**| **2.94**| **18585**| **2.44**| **21251**| **2.04**|
## Weakness
**Response to W1:**
- **ROS-vanilla** (without pre-training) can directly generalize to any value of $k$ since the absence of pre-training.
- **ROS** (with pre-training and fine-tuning) improves efficiency but does not generalize directly to unseen $k$ due to the fixed output layer during pre-training. However, this limitation can be addressed through **ROS-partial**, a simple modification that enables adaptation to different $k$.
- **ROS-partial** works by pre-training the model on $k=2$ while saving all parameters except the last layer. Before fine-tuning, the pre-trained parameters are loaded, and the last layer is randomly initialized to accommodate the new $k$. This approach serves as a middle ground between ROS (fully pre-trained) and ROS-Vanilla (no pre-training).
- We evaluate **ROS-partial**, **ROS**, and **ROS-vanilla** on the Bitcoin-OTC dataset. The results in Table 2 show that ROS-partial effectively generalizes to different $k$ while maintaining strong performance.
**Table 2: Comparison between pre-training ways on Bitcoin-OTC Datasets.**
| Model | Value ($k=2$) | Time (s) ($k=2$) | Value ($k=3$) | Time (s) ($k=3$) | Value ($k=10$) | Time (s) ($k=10$) |
| - | - | - | - | - | - | - |
| ROS| 15384| **2.94**| 18585| **2.44**| 21251| **2.04**|
| ROS-vanilla| **15661**| 5.24| **18977**| 4.77| **21365**| 4.43|
| ROS-partial| 15102| 4.24| 18732| 3.93| 21308| 2.92|
**Response to W2:**
- The pre-training and fine-tuning phases of ROS correspond to the training and inference phases of other L2O baselines. Specifically, ROS is pre-trained on a collected dataset, similar to how L2O baselines are trained. During fine-tuning, ROS further optimizes based on **test instances**, whereas standard L2O inference keeps parameters fixed. To ensure fairness, we include the full fine-tuning time in our reported results. Thus, the datasets used for pre-training (training) and fine-tuning (testing) in ROS align with those in other L2O methods.
- To further address the concern, we also conduct experiments where we introduce fine-tuning to existing L2O baselines. After training, these models are further fine-tuned on test instances, and we plot the cut value against fine-tuning iterations in the [anonymous link](https://anonymous.4open.science/r/Figures_for_bfPu-9473). The results confirm that even with fine-tuning, other baselines do not surpass ROS in solution quality.
**Response to W3:** We upload our code in https://anonymous.4open.science/r/ROS_anonymous-1C88/.
## Reference
[1] Rishi Rajesh Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya and Sayan Ranu, "NeuroCut: A Neural Approach for Robust Graph Partitioning", in KDD, 2024.
[2] S. Kumar, F. Spezzano, V.S. Subrahmanian, C. Faloutsos. Edge Weight Prediction in Weighted Signed Networks. IEEE International Conference on Data Mining (ICDM), 2016.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for additional experiments.
Could you clarify what was the objective used for NeuroCUT in this experiment.
Further, the node selection heuristic I believe could be kept random in this case.
I would expect clarification on how was NeuroCUT was integrated just to ensure comparison is fair.
I am happy to see running time results. ROS is significantly faster than all methods.
Although generalization to k is hacky, but happy to see the results.
---
Reply to Comment 1.1.1:
Comment: > **Comment:** I thank the authors for additional experiments. Could you clarify what was the objective used for NeuroCUT in this experiment. Further, the node selection heuristic I believe could be kept random in this case. I would expect clarification on how was NeuroCUT was integrated just to ensure comparison is fair. I am happy to see running time results. ROS is significantly faster than all methods. Although generalization to k is hacky, but happy to see the results.
**Reply:** We appreciate your efforts in reviewing our paper and rebuttal, and thank you for your valuable feedback.
- To implement NeuroCUT, we used the loss function defined in problem $(P)$ (line 131, right column), as the source code of NeuroCUT minimizes the objective.
- To ensure a fair comparison, we replaced the original score-based node selection heuristic with random selection, as suggested.
- Additionally, we found that the original K-means initialization is designed for graph clustering, and applying it to Max-$k$-Cut often leads to suboptimal starting points, even worse than random initialization. Therefore, we replaced it with random initialization.
The updated results on Bitcoin-OTC are included in the following table.
**Updated Table 1: Updated Evaluation results on Bitcoin-OTC Datasets. Here, NeuroCut is equipped with random initialization and random node selection, which is different from the previous Table 1.**
| Model | Value ($k=2$) | Time (s) ($k=2$) | Value ($k=3$) | Time (s) ($k=3$) | Value ($k=10$) | Time (s) ($k=10$) |
| - | - | - | - | - | - | - |
| NeuroCut| 10260 | 240.98 | 10896 | 237.09 | 17768 | 249.99 |
| PIGNN| 14587| 62.31| -| -| -| -|
| MD| 14989| 37.15| 18448| 50.40| 21182| 105.92|
| ANYCSP| 10678| 180.20| 14319| 180.16| 19359|180.24|
| ROS| **15384**| **2.94**| **18585**| **2.44**| **21251**| **2.04**|
Regarding the generalization to unseen $k$, we provide two approaches based on the "pre-training + fine-tuning" framework of ROS:
- **ROS-vanilla**: This method is directly fine-tuned on the test instance without pre-training, avoiding dependency on predefined last-layer dimensions.
- **ROS-partial**: To apply the pre-training technique and improve efficiency while still generalizing to unseen $k$, this variant is pre-trained on $k=2$ while saving all parameters except the last layer. Before fine-tuning, the pre-trained parameters are loaded, and the last layer is randomly initialized to accommodate the new $k$.
As shown in Table 2 of the rebuttal, both approaches demonstrate the **flexibility and extensibility** of our "pre-train + fine-tune" framework of ROS. Furthermore, while our framework supports generalization to unseen $k$, we acknowledge that exploring this aspect through model architecture design, as in [1], is an exciting direction.
We appreciate your valuable comments once again.
[1] NeuroCUT: A Neural Approach for Robust Graph Partitioning Rishi Shah, Krishnanshu Jain, Sahil Manchanda, Sourav Medya, Sayan Ranu KDD Knowledge Discovery and Data Mining(KDD), 2024. | Summary: The paper proposes a GNN-based solver for the mak-k-cut problem.
Claims And Evidence: Yes. But I do have many questions.
Methods And Evaluation Criteria: Some points may not be clear enough. For example,
- Does other baselines use the same training data as the training+finetuning datasets of ROS? If not, can other methods be fit under the pretrain-finetune framework?
Theoretical Claims: I did not check them very carefully.
Experimental Designs Or Analyses: See comments.
Supplementary Material: I have checked the appendix D. The proofs were not checked detailedly.
Relation To Broader Scientific Literature: The work contributes to the combinatorial optimization community.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: Strengths
- The max k cut problem, as a generalization of the max cut problem, holds significant research value.
Weaknesses
- The scope of the paper is relatively narrow. The proposed framework is only applicable to the max k cut problem. It would be more meaningful if the framework could be more widely applied to other combinatorial optimization problems.
- The method appears to lack novelty. The pretrain-finetune framework employed is not new and has been widely used in other contexts.
- The comparison with baseline methods may not be entirely fair. I question whether the training data used are consistent with those used in ROS. Given that ROS involves a two-stage process of pretraining and finetuning, whereas other methods only include a single training step, this discrepancy could affect the validity of the comparisons.
- I find the experimental section somewhat challenging to follow. The descriptions of the experimental settings are somewhat disorganized and could benefit from clearer and more structured presentation.
- The absence of a related works section is notable. While it is true that research on the max k cut problem may be relatively sparse, it is still unusual to omit this section entirely. Including a discussion of related works would provide valuable context and help situate the current research within the broader field.
Other Comments Or Suggestions: - Fig. 1 has two h6 in the initialization step of the grey box
- Notations are sometimes abused. For example, \overline{X} shows up three times with different meanings. In Def 3.1, it is a point. In Theorem 3.2, it is the globally optimal solution. In Q2, it is a high quality solution. They make me confused.
- Statistics of the datasets are not given. For example, how many graphs are in the different datasets?
- In the results of figure 2, which part of the datasets are used for training, which part are for finetuning, and which part are for testing? It seems that Sec. 4.1 does not figure it out.
Questions For Authors: - Noticing that the initial embeddings h0 are assigned by random values. I have doubt on the correctness of doing so.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Methods And Evaluation Criteria
**Response to M1:** Please see "Response to W2" for Reviewer bfPu.
## Weakness
**Response to W1:** The Max-$k$-Cut problem is a fundamental NP-complete problem with applications in physics [1], power networks [2], and data clustering [3]. While ROS is tailored for Max-$k$-Cut, its core Relax-Optimize-and-Sample framework is generalizable to other combinatorial optimization problems by adjusting the objective functions. Investigating such extensions, particularly their theoretical guarantees, is a promising direction for future work.
**Response to W2:** The core novelty of our work lies in the Relax-Optimize-and-Sample (ROS) framework, where the "pre-train + fine-tune" approach is used solely for efficiency. The key contributions of ROS are:
- The probability simplex relaxation ensures that the optimal values of the relaxed and original Max-$k$-Cut problems are equivalent (Theorem 3.2).
- A GNN parametrizes the decision variable, enhancing both representation power and computational efficiency.
- The proposed sampling procedure maps the relaxed solution to a discrete Max-$k$-Cut solution while preserving the objective value (Theorem 3.3).
**Response to W3:** Please see "Response to W2" for Reviewer bfPu.
**Response to W4:** We will refine and reorganize the experimental section to improve clarity and readability. Specifically, we will integrate Tables 2 and 3 in [anonymous link](https://anonymous.4open.science/r/Tables_and_Reference_For_zJRF-9D0B) into the manuscript to provide a clearer presentation of dataset statistics and enhance the overall structure of the experimental setup.
**Response to W5:** We will add a Related Work section to provide context. This will cover approximation algorithms (e.g., Goemans-Williamson (GW) [4], Frieze et al. [5]), non-convex relaxations (Rank-2 [6], QUBO [7]), and Lovász extensions [8]. We will clarify how ROS differs by ensuring objective value consistency and leveraging GNN-based optimization for high-quality solutions. We will also add Table 1 in [anonymous link](https://anonymous.4open.science/r/Tables_and_Reference_For_zJRF-9D0B) to further clarify the distinctions between these methods.
## Other Comments and Suggestions:
**Response to C1 and C2:** We will revise Fig. 1 to correct the typo and ensure that all notations are used consistently throughout the manuscript.
**Response to C3:** The statistics of the training and testing datasets are summarized in Tables 2 and 3 in [anonymous link](https://anonymous.4open.science/r/Tables_and_Reference_For_zJRF-9D0B), which we will add to the manuscript for clarity.
**Response to C4:** The training dataset consists of 500 3-regular graphs for $k=2$ and 500 5-regular graphs for $k=3$. The fine-tuning (testing) datasets correspond to different graph types: (a) random regular graphs, (b) Gset, and \(c) weighted Gset, as detailed in Section 4.1 (Line 272, right column, Page 5).
## Questions For Authors
**Response to Q1:**
- The random initialization does not introduce instability, as shown by the low standard deviation in Table 1 in manuscripts, where the relative error across runs remains around 1%.
- Additionally, the node features and the adjacency information can be incorporated as initialization in ROS when it is available. For example, on the Cora dataset [9], we interpolated both node features as well as the adjacency matrix to match the input dimension. Results in Table 4 in the [anonymous link](https://anonymous.4open.science/r/Tables_and_Reference_For_zJRF-9D0B) show that when all other model parameters remain the same, the model yields identical outputs across different initialization methods, confirming the adequacy of random initialization.
- Furthermore, random initialization facilitates distributed deployment where each node is employed on a different device, avoiding global operations required for feature interpolation.
## Reference
See [anonymous link](https://anonymous.4open.science/r/Tables_and_Reference_For_zJRF-9D0B). | null | null | null | null | null | null |
Retrieval-Augmented Language Model for Knowledge-aware Protein Encoding | Accept (poster) | Summary: The paper presents Kara, a knowledge-aware retrieval-augmented protein language model, designed to explicitly integrate knowledge from protein knowledge graphs (PKGs) into protein language models (PLMs). Unlike previous methods that implicitly embed knowledge, Kara directly injects structured knowledge through contextualized virtual tokens, allowing seamless knowledge integration during both pre-training and fine-tuning. A knowledge retriever dynamically retrieves gene descriptions for new proteins, ensuring the model continuously adapts to knowledge updates. Extensive experiments across six protein-related tasks demonstrate that Kara consistently outperforms existing knowledge-enhanced models by effectively capturing high-order biological relationships.
## update after rebuttal
The author responses address most of my concerns. I will keep my positive rating.
Claims And Evidence: Overall, the paper's main claims are mostly supported by experimental evidence, but some key assumptions require further verification.
Well-supported claims:
1. Kara outperforms existing knowledge-enhanced PLMs (e.g., KeAP, OntoProtein) across six protein-related tasks. The paper provides comprehensive evaluations and ablation studies showing consistent improvements.
2. Kara effectively mitigates catastrophic forgetting by integrating knowledge into both pre-training and fine-tuning. The use of a knowledge retriever ensures continuous knowledge updates, which static models lack.
3. Explicit knowledge injection and high-order structure modeling enhance PLM performance. The introduction of contextualized virtual tokens improves knowledge integration and retrieval efficiency.
Claims needing stronger justification:
1. The advantage of direct knowledge injection over implicit embedding is not clearly isolated. A controlled experiment comparing models with virtual tokens but without retrieval is needed to confirm its impact.
2. This paper lacks visualization or biological case studies to demonstrate how Kara's representations align with real-world protein functions.
Methods And Evaluation Criteria: The proposed methods are well-designed for integrating knowledge into protein language models and offer several unique advantages.
1. Unlike previous models that only inject knowledge during pre-training, Kara ensures continuous knowledge updates via retrieval, preventing catastrophic forgetting.
2. Contextualized virtual tokens enable direct knowledge and structure fusion. By representing gene ontology (GO) annotations and functionally similar proteins as learnable tokens, Kara effectively integrates biological insights at the sequence level.
3. Knowledge retriever dynamically aligns new proteins with the knowledge graph. Instead of relying on static embeddings, Kara retrieves relevant gene descriptions for unseen proteins, improving generalization.
4. Six tasks are well-chosen to assess Kara’s ability to model sequence-function relationships, demonstrating its applicability to real-world biological challenges.
Theoretical Claims: The paper primarily focuses on methodological innovations rather than formal theoretical derivations. The key claims rely on empirical results rather than mathematical proofs. The loss functions and optimization strategies, such as structure-based regularization, are well-defined and align with standard machine learning principles.
Experimental Designs Or Analyses: Strengths of experimental designs/analysis:
1. The six protein-related tasks cover both structural and functional modeling, ensuring practical relevance.
2. Ablation studies show that removing virtual tokens, retrieval, or structure-based regularization leads to performance drops, proving their importance.
Limitations:
1. The study does not evaluate Kara on low-identity or novel proteins, making its generalization unclear.
2. Only ProtBert is tested as the encoder, without comparisons to models like ESM-1b, limiting generalizability.
Supplementary Material: I reviewed the dataset description, downstream task definitions, and experimental details. The supplementary material provides essential information for reproducibility, including dataset selection, training configurations, and evaluation metrics.
Relation To Broader Scientific Literature: This paper builds on prior work in protein language modeling and knowledge-enhanced machine learning. It follows models like OntoProtein and KeAP, which integrate protein knowledge graphs (PKGs) into language models, but differs by introducing explicit knowledge injection through contextualized virtual tokens and a knowledge retriever. This aligns with trends in retrieval-augmented language models, similar to approaches in retrieval-based NLP models that dynamically fetch external knowledge. The use of structure-based regularization is also inspired by contrastive learning methods, commonly used in representation learning to enforce semantic consistency. While Kara advances knowledge integration in PLMs, it does not explore multimodal protein representations (e.g., 3D structures), which have gained traction in recent biological AI research.
Essential References Not Discussed: I have already mentioned the missing related research in the previous question “Relation To Broader Scientific Literature”.
Other Strengths And Weaknesses: Kara improves protein language models with structured knowledge, making it highly relevant to biological AI. It creatively integrates retrieval, virtual tokens, and structure-based regularization to enhance knowledge utilization. The paper is well-structured and clearly explains the methods, experiments, and results.
However, the approach closely follows retrieval-based NLP models and does not introduce fundamentally new ML architectures. The paper also does not discuss how Kara performs on novel proteins with missing or incomplete knowledge.
Other Comments Or Suggestions: See above.
Questions For Authors: Please refer to the previous sections for key points regarding Claims and Evidence, Methods and Evaluation Criteria, Experimental Designs or Analyses, etc.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: __Thanks for your kind comments, we place all tables and figures in this anonymous link(https://anonymous.4open.science/r/Rebuttal-F1C0/README.md)__
``W1. Claims needing stronger justification: (1) The advantage of direct knowledge injection over implicit embedding is not clearly isolated. A controlled experiment comparing models with virtual tokens but without retrieval is needed to confirm its impact.
(2) This paper lacks visualization or biological case studies to demonstrate how Kara's representations align with real-world protein functions.``
(1) Thanks for your kind comment. Here, we present the performance of different models for proteins within knowledge graphs. For Kara with virtual tokens but without retrieval, we construct virtual tokens using the ground-truth knowledge of each protein from the knowledge graph. In contrast, the original Kara employs a retriever to predict relevant knowledge for virtual token construction.
As shown in Table 10, the variant without retrieval outperforms KeAP and OntoProtein, which embed knowledge implicitly, demonstrating the advantage of direct knowledge injection. Furthermore, the original Kara achieves performance comparable to the variant without retrieval, which utilizes ground-truth knowledge. This result highlights the effectiveness of the proposed retriever in accurately predicting protein knowledge.
(2) We have provided a visualization case study comparing Kara and KeAP on the contact prediction task in "case_study_Figures.png". The results indicate that Kara outperforms KeAP in predicting contacts for proteins with short sequences (e.g., cases 1, 4, 5, and 7). However, as the sequence length increases, both Kara and KeAP struggle to accurately align with the ground truth contact map (e.g., cases 2, 3, and 6). This limitation may stem from the lack of protein structural information modeling, which is crucial for effectively handling long-sequence proteins.
``W2. The study does not evaluate Kara on low-identity or novel proteins, making its generalization unclear.``
We would like to clarify, as stated in Appendix B (Lines 637–639), that we removed all proteins appearing in the downstream task datasets from the protein knowledge graph. Consequently, during inference, all proteins in the downstream tasks were unseen during training, and no related knowledge existed in the knowledge graph. Therefore, all results presented in the original paper reflect the model's performance on unseen proteins. The significant advantage of Kara over existing models demonstrates its strong generalization ability to unseen proteins.
``W3. Only ProtBert is tested as the encoder, without comparisons to models like ESM-1b, limiting generalizability.``
We would like to clarify that Table 7 in the original paper already presents the performance of Kara using different encoders, including ProtBert, ProteinBert, and ESM-1b.
``W4. The approach closely follows retrieval-based NLP models and does not introduce fundamentally new ML architectures.``
Thanks for your kind comment. As we have discussed in Appendix C (Lines 643-668), there are several key differences between our model and the retrieval-based NLP models, highlighting our model as an enhanced paradigm for integrating protein knowledge graphs into protein language models.
(1) NLP approaches using virtual tokens assume that all encoding objectives exist in a knowledge graph, allowing direct extraction of relevant information. However, this assumption fails in protein encoding, where many proteins are absent from KGs. Our model addresses this by introducing a knowledge retriever that predicts gene descriptions for unseen proteins, enabling generalization beyond predefined KG entities.
(2) Existing retriever-based NLP models use general KGs but cannot account for the unique complexities of protein KGs. Protein KGs contain multi-modal entity types requiring specialized retrieval mechanisms, and they contain large and complex gene descriptions, making the retrieval time-consuming. Our model overcomes these challenges through multi-modal matching loss and relation-go combination strategies.
(3) Previous retriever-based NLP models primarily target document encoding, where KG entities are words within text corpora. These methods fail in protein encoding, since both the encoding objective and KG entities are protein sequences. Moreover, they only incorporate one-hop neighbors, overlooking higher-order structural relevance critical for protein functionality. Our model incorporates structure-based regularizations to address these limitations. | Summary: This article proposes a knowledge-aware retrieval-augmented protein language model named Kara. During the pre-training phase, it extracts structural and knowledge information from protein KGs through contextualized virtual tokens, which are jointly embedded into the protein sequence encoding. The optimization objectives of both the pre-training and fine-tuning stages are unified through structure-based regularization. In the fine-tuning stage, a knowledge retriever predicts potential GO representations for new proteins within the PKG, thereby alleviating the issue of catastrophic forgetting of knowledge that has plagued previous models. Across multiple downstream tasks in protein prediction, Kara surpasses the current state-of-the-art models.
Claims And Evidence: Yes. The experimental design and ablation study validated the effectiveness of the model and the necessity of each structure.
Methods And Evaluation Criteria: The six experimental datasets and Tape benchmark mentioned in the article are commonly used prediction datasets in the field of protein language modeling. Protein language models have practical significance for predicting the properties and functions of newly discovered proteins. However, the baselines used in the paper should include more recent papers.
Theoretical Claims: There is no theoretical claims.
Experimental Designs Or Analyses: Yes. The article conducts comprehensive experiments on multiple tasks of protein prediction. It performs three independent experiments and takes the average to avoid the impact of randomness. Data partitioning also adheres to previous works, such as removing overlapping proteins between the training and test sets, ensuring the accuracy of the experiments. The results reported in the tables and figures can be more cafully compared to state-of-the-art.
Supplementary Material: Yes. I carefully reviewed the explanations for the knowledge graph and datasets in the supplementary materials.
Relation To Broader Scientific Literature: The article extensively cites relevant protein models (such as ProtBert, ESM) and knowledge-enhanced methods (including OntoProtein, KeAP), and provides detailed experimental comparisons.
Essential References Not Discussed: The technical elements in this paper are easy to follow, and no more references are in need to make the paper more readable.
Other Strengths And Weaknesses: Firstly, it introduces a dynamic retrieval mechanism from general language models into protein language models, supporting the dynamic updates of knowledge graphs, which is suitable for the rapid iteration needs in the biomedical field. The main issue is that combining retrieval information with sequence encoding lacks innovation and does not explore deeper graph structures.
Other Comments Or Suggestions: No.
Questions For Authors: Have you considered applying retrieval augmentation directly to the inference stage instead of using the retriever only in the fine-tuning phase?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: __Thanks for your kind comments, we place all tables and figures in this anonymous link(https://anonymous.4open.science/r/Rebuttal-F1C0/README.md)__
``W1. The baselines used in the paper should include more recent papers.``
Thanks for your kind comment. As shown in Table 1, we compare the performance of Kara with more recent and powerful models, SaProt [1] and ProSST [2], on the ProteinGYM benchmark. Kara, with the ESM2 backbone, performs competitively with SaProt but falls short of ProSST due to the lack of structural information. In the inductive setting, where test proteins are unseen and no structural or prior knowledge is available, Kara outperforms both models (Table 2). This is because Kara can automatically align unseen proteins with the protein knowledge graph through the retriever, thus enhancing generalization. In contrast, SaProt and ProSST perform poorly as they heavily rely on manually curated protein structures.
[1] ProSST: Protein Language Modeling with Quantized Structure and Disentangled Attention. NuerIPS 2024
[2] SaProt: Protein Language Modeling with Structure-aware Vocabulary. ICLR 2024
``W2. Combining retrieval information with sequence encoding lacks innovation and does not explore deeper graph structures.``
Thanks for your kind comment. Firstly, our model is not a simple combination of retrieval information with sequence encoding, it aims to address three key technical problems for knowledge-aware protein encoding:
(1) KGs are consistently updated in the real world, how to avoid the model using outdated knowledge?
(2) Many newly observed proteins are understudied and thus do not exist in KG. How can we generalize the model to these understudied proteins?
(3) Usually, we need to fine-tune the model to adapt to various downstream applications. How can we ensure the knowledge learned during pre-training is not to be catastrophically forgotten during fine-tuning?
To address these problems, many protein modeling-specific challenges arise, such as how to align multiple modalities of information in protein knowledge graphs, how to scale the retriever to large-scale protein knowledge graphs, and how to unify the knowledge pre-training and task-oriented fine-tuning optimization objectives. The proposed Kara is incorporated with new methodologies designed especially to address these challenges. We propose a knowledge retriever to solve the modality alignment and scaleability challenges through multi-modal matching loss and relation-go combination strategies, and the contextualized virtual tokens with structure-based regularization are proposed to unify knowledge modeling during pre-training and fine-tuning.
In summary, Kara contains several unique technical designs (e.g., knowledge retriever and structure-based regularizations) to solve special challenges in protein encoding scenarios, making it different from previous methods.
Second, our model has incorporated both first-order and second-order graph structures, as these local structures contain the most informative knowledge for a protein. We agree that exploring more complex graph structures is an interesting direction, but given the increased retrieval complexity, we tend to consider this in future research.
``W3. Have you considered applying retrieval augmentation directly to the inference stage instead of using the retriever only in the fine-tuning phase?``
We have to clarify that the proposed Kara does not use the retriever only in the fine-tuning phase, instead, it uses the retriever both during fine-tuning and inference. During fine-tuning, the retriever is used to align downstream proteins with the knowledge graph, thus unifying the pre-training and fine-tuning objectives. During inference, the retriever is used to predict potential knowledge descriptions for unseen proteins, and thus explicitly integrate knowledge for protein encoding. Table 4 presents the model’s performance when the retriever is removed during fine-tuning or inference. The results show a substantial performance drop of Kara in the absence of the retriever, highlighting the critical role of the retriever in the effective knowledge integration. | Summary: This paper proposes Kara, a knowledge-aware retrieval-augmented language model for protein representation learning, explicitly integrating protein knowledge graphs (PKGs) with protein language models (PLMs). The key innovation lies in using contextualized virtual tokens and a knowledge retriever, allowing explicit integration of structured and task-specific knowledge during both pre-training and fine-tuning phases. The model demonstrates superior performance across multiple downstream protein tasks, including amino acid contact prediction, protein-protein interaction (PPI) prediction, homology detection, and protein stability prediction, surpassing existing baselines (e.g., ProtBert, OntoProtein, KeAP) with significant margins.
## Update after rebuttal
I appreciate the authors' comprehensive and thoughtful rebuttal. The additional experiments, including the case study on contact prediction, robustness evaluation on alternate knowledge graphs, and further clarification on catastrophic forgetting, were informative and addressed most of my earlier concerns.
The strategy to mitigate catastrophic forgetting—via explicit virtual token design and continual alignment through the knowledge retriever—is clearly explained and well-supported by the updated results. I also found the scalability discussion reassuring in terms of Kara’s practicality for large-scale knowledge graphs.
That said, there is still room for **deeper empirical error analysis** and **broader generalizability validation on different KGs**. These are directions that could further improve the work, but do not critically undermine the current contribution.
Overall, I keep my score of 3.
Claims And Evidence: Most claims are well-supported by comprehensive evidence from the experiments:
1. The explicit integration of knowledge graphs into PLMs significantly enhances downstream protein representation tasks (see Tables 1, 2, and 3).
2. Contextualized virtual tokens effectively incorporate graph structures and gene ontology information, as demonstrated by the ablation studies (refer to Table 6).
However, the following claim requires further clarification:
- Claim: Kara effectively avoids catastrophic forgetting due to the unified integration of knowledge across training stages.
This claim is partially supported, as shown in Table 2 and Table 8. However, more insights and case studies are needed to illustrate scenarios of catastrophic forgetting. What is the formal definition of catastrophic forgetting? Does it refer to the decline in performance of a Protein LM when fine-tuned on a large number of data?
Methods And Evaluation Criteria: The proposed methods and evaluation criteria align well with standard practices in protein representation learning.
1. **Methodology**:
- Clearly detailed, integrating knowledge via contextualized virtual tokens.
- Incorporates structure-based regularization (Section 3) is appropriate.
2. **Evaluation Criteria**:
- Includes different metrics for each downstream tasks, which are comprehensive.
- Choice of downstream evaluation tasks is suitable and diverse.
Theoretical Claims: The paper makes no explicit theoretical claims, thus no theoretical evaluation is required.
Experimental Designs Or Analyses: **Strengths:**
1. A robust experimental design that includes multiple relevant downstream tasks and thorough comparisons with various competitive baselines.
2. It features ablation studies that clearly illustrate the contributions of different components in the model.
**Weaknesses:**
1. There is a limited examination of how sensitivity varies based on the quality or completeness of the knowledge graph. Empirical studies that specifically analyze the effects of knowledge graph incompleteness or noise are lacking. It would be beneficial to test a different protein knowledge graph to determine if the proposed method is generalizable.
2. There is a lack of comprehensive error analysis, particularly in situations where Kara underperforms or fails.
Supplementary Material: I carefully reviewed the appendices, and everything appears to be in order. To enhance comprehension of Kara's performance, it would be helpful to include specific examples of both successful and unsuccessful knowledge graph retrieval scenarios. Additionally, incorporating instances of virtual token creation and failed predictions would provide further clarity.
Relation To Broader Scientific Literature: The proposed method builds upon existing literature, situating itself within knowledge-enhanced protein language modeling (e.g., OntoProtein, KeAP). It explicitly extends prior work by incorporating structured, task-oriented knowledge into the fine-tuning and inference phases of PLM.
Essential References Not Discussed: I am not aware of any essential references being missing. I think the author did a great job in Appendix C discussing the differences compared to retrieval-augmented LMs in other fields.
Other Strengths And Weaknesses: **Strengths:**
- Methodologically innovative, with a clear integration of knowledge graphs and PLMs.
- Strong empirical validation showing consistent improvements across a variety of downstream tasks.
- Clearly communicates the methodological advantages and potential real-world biological implications.
**Weakness:**
- The discussion does not address computational overhead and the practical scalability of very large-scale protein knowledge graphs.
Other Comments Or Suggestions: 1. Propose a deeper analysis of robustness against incomplete or noisy PKGs, including:
- Edge dropout experiments
- Perturbation experiments
2. Recommend the following for real-world deployment:
- Exploration of computational overhead
- Scalability analysis
Questions For Authors: If the authors could provide insights into the questions raised in the previous sections and the below questions, I would be happy to consider raising the score.
1. Could you provide explicit evidence or case studies on scenarios of catastrophic forgetting, as well as more insights on how Kara mitigates these issues?
2. How sensitive is Kara to errors or noise in the predictions made by the knowledge retriever in the finetuning stage?
3. Have you tested Kara's robustness with varying qualities of textual descriptions associated with GO entities? How does performance change based on the quality of these descriptions?
4. Can you discuss the practical scalability of very large-scale protein knowledge graphs?
5. Could you provide a case study for error analysis, particularly when Kara underperforms or encounters failures?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: __Thanks for your kind comments, we place all tables and figures in this anonymous link(https://anonymous.4open.science/r/Rebuttal-F1C0/README.md)__
``W1. The following claim requires further clarification: Kara effectively avoids catastrophic forgetting due to the unified integration of knowledge across training stages.``
We would like to clarify that "catastrophic forgetting" in this context refers to the loss of protein attribute knowledge learned during pretraining on the protein knowledge graph due to parameter updates during downstream fine-tuning.
To evaluate Kara’s effectiveness in mitigating catastrophic forgetting, we designed two experiments. The first measures the similarity between the embeddings of two proteins with the same attribute knowledge—a higher cosine similarity indicates better retention of knowledge information. The second requires the model to identify, from a set of candidate proteins, the one sharing attribute knowledge with a given protein. Higher accuracy suggests better embedding and preservation of knowledge information.
As shown in Table 5, OntoProtein, Keap, and Kara all perform well after pretraining, confirming their ability to learn attribute knowledge. Kara achieves the highest performance, demonstrating its superior knowledge acquisition capability. After fine-tuning on downstream tasks, Kara’s performance remains stable, whereas OntoProtein and Keap show significant drops, indicating that they lose some of the knowledge acquired during pretraining. Furthermore, removing the structure loss or virtual token leads to performance degradation after fine-tuning, highlighting the importance of unified knowledge integration in mitigating catastrophic forgetting.
``W2. There is a limited examination of how sensitivity varies based on the quality or completeness of the knowledge graph.``
First, we have to clarify that Table 8 in the original paper already analyzes the performance of different models when dealing with incomplete knowledge graphs (Edge dropout experiments). For retrieval noises analysis (Perturbation experiments), please refer to Reviewer rtvB-Q2. In Table 9, we provide the performance of Kara with ProteinKG65, showing its generalization ability to different knowledge graphs.
``W3. There is a lack of comprehensive error analysis, particularly in situations where Kara underperforms or fails.``
Thank you for your thoughtful comment. We have provided a visualization case study comparing Kara and KeAP on the contact prediction task in "case_study_Figures.png". The results indicate that Kara outperforms KeAP in predicting contacts for proteins with short sequences (e.g., cases 1, 4, 5, and 7). However, as the sequence length increases, both Kara and KeAP struggle to accurately align with the ground truth contact map (e.g., cases 2, 3, and 6). This limitation may stem from the lack of protein structural information modeling, which is crucial for effectively handling long-sequence proteins.
``W4. Computational overhead and the practical scalability of very large-scale protein knowledge graphs``
As discussed in lines 263–274 on page 5, we designed the relation-GO combinations strategy to generalize to large-scale KGs. Table 6 presents the time cost of Kara during training and inference with and without the retriever. The results show that, after applying the relation-GO combinations strategy, Kara's training and inference time only slightly increases compared to knowledge-free baselines (even on large-scale knowledge graph ProteinKG65), demonstrating its scalability.
``Q1. More insights on how Kara mitigates catastrophic forgetting.``
Existing approaches like KeAP and OntoProtein employ knowledge graph-supervised pre-training to encode knowledge information into model parameters, followed by task-specific fine-tuning using proteins from downstream tasks. However, the absence of knowledge descriptions for proteins in downstream tasks creates a knowledge supervision gap during fine-tuning. This causes the model optimization to focus solely on task objectives, potentially overwriting the previously acquired knowledge representations in parameters and leading to catastrophic knowledge forgetting.
In contrast, our proposed Kara framework addresses these issues through two key innovations. First, rather than implicitly storing knowledge in model parameters, Kara explicitly incorporates knowledge through virtual tokens. This architectural design decouples knowledge storage from model parameters, making the acquired knowledge resilient to parameter updates during downstream fine-tuning. Second, Kara introduces a knowledge retriever that aligns downstream task proteins with the knowledge graph to predict potential knowledge descriptions. This alignment mechanism enables continuous knowledge supervision during fine-tuning, ensuring that parameter updates simultaneously optimize for both task performance and knowledge consistency.
---
Rebuttal Comment 1.1:
Comment: Thanks for your response, which addresses the majority of my concerns. I will keep the current positive score. | Summary: The paper presents Kara, a knowledge-aware retrieval-augmented protein language model that explicitly integrates protein knowledge graphs (PKGs) with protein language models (PLMs), enhancing protein representation learning with task-specific knowledge and graph structure information.
Kara predicts potential gene descriptions for proteins (via knowledge retriever), aligning them with PKGs before injecting the task-relevant high-order graph structure information into protein representations with contextualized virtual tokens.
They propose the use of structure-based regularization to maintain consistency between pre-training and fine-tuning objectives.
Kara outperforms existing models like knowledge-enhanced PLMs KeAP** and ESM-2 across six downstream tasks.
The paper proposes different ablation studies, e.g., the effectiveness of each component, numbers of knowledge, and knowledge retriever.
Claims And Evidence: 1. The main claim of the paper (*Kara improves protein function modeling by explicitly incorporating task-oriented knowledge*) is clear and supported by empirical evidence.
* Kara outperforms KeAP and ESM-2 across six benchmark tasks, e.g., Kara achieves 11.6$\%$ improvement in long-range contact prediction.
* Stronger baselines may be considered (though they utilize further protein structural information) like SaProt (https://openreview.net/forum?id=6MRm3G4NiU) or ProSST (https://www.biorxiv.org/content/10.1101/2024.04.15.589672v3), which shows to achieve higher performance, e.g., on contact prediction. Furthermore, it seems the ESM2 performance reported in SaProt (Table 3) for contact prediction is higher than the scores in this paper.
2. The following claims are clear and intuitive but require further evidence to be strongly supported.
- (1) The knowledge retriever enhances generalization to unseen proteins.
- (2) Kara mitigates catastrophic forgetting through unified knowledge integration.
3. The ablation studies confirm the contributions of virtual tokens, structure-based regularization, and retrieval mechanisms.
However, an error analysis on the effect of the retriever on the performance when it introduces incorrect knowledge
Methods And Evaluation Criteria: **Methods**
- The proposed framework is sound and intuitive.
- However, it should indicate the assumptions in which the method works: (i) Relevant knowledge for a protein exists in the PKG, (ii) Graph structure provides meaningful relationships.
**Evaluation**
- The benchmark is comprehensive (amino acid contact prediction, PPI identification, homology detection, stability prediction). However, the fitness prediction (zero-shot) for PLMs should be considered together with perplexity to validate that the model prevents forgetting.
- Ablation studies validate each component’s contribution and provide insights into retrieval behavior.
- Baselines: As mentioned above, the paper may consider the latest baselines that show higher performance on these tasks.
Theoretical Claims: No theoretical claim.
Experimental Designs Or Analyses: Yes, I checked all experiments for 6 downstream tasks and ablation studies.
Supplementary Material: Yes, all parts.
Relation To Broader Scientific Literature: - The problem of knowledge-aware protein representation learning is highly relevant to current works of protein language model and computational biology.
- The paper clearly articulates the limitations of previous methods and proposes a novel retrieval-based augmentation.
Essential References Not Discussed: No
Other Strengths And Weaknesses: **Strengths**:
- The problem of interest is interesting and timely.
- The proposed method is sound and useful for further research on PLMs.
- The paper is well-structured
**Weaknesses**:
- Kara depends on the retriever. If the retriever selects incorrect gene descriptions, it may degrade performance rather than improve it.
- The retrieval complexity scales better than brute-force retrieval, but it is unclear how well it generalizes to large-scale PKGs, which serves the purpose of the paper. Furthermore, how does the retrieval overhead compare to knowledge-free baselines?
Other Comments Or Suggestions: - The "limitations" in the introduction may cause a misunderstanding as to the limitations of this work. The writing of this part can be polished for better understanding with cited evidence.
- Some sections are very dense, e.g., 3.2 and 3.3, with some repetitive/unnecessary information/notations that can be trimmed for better readability.
Questions For Authors: 1. What happens when the retrieval mechanism introduces incorrect or irrelevant gene descriptions? How does noisy or incomplete PKG knowledge affect the model?
2. Can retrieval be extended to handle proteins with missing or sparse knowledge? What happens when a protein has no useful GO entities?
3. Instead of fixed K retrieved entities, could a confidence-based retrieval mechanism improve accuracy? Is there a trade-off between retrieval depth and performance?
4. Given the proteins in the PKGs for inference, can you elaborate why explicitly using knowledge (as of Kara) is better then the one encoded in pretraining?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: __Thanks for your kind comments, we place all tables in this anonymous link(https://anonymous.4open.science/r/Rebuttal-F1C0/README.md)__
``W1. Stronger baselines may be considered.``
As shown in Table 1, we compare the performance of Kara, SaProt, and ProSST on the ProteinGYM benchmark. Kara, with the ESM2 backbone, performs competitively with SaProt but falls short of ProSST due to the lack of structural information. In the inductive setting, where test proteins are unseen and no structural or prior knowledge is available, Kara outperforms both models (Table 2). This is because Kara can automatically align unseen proteins with the protein knowledge graph through the retriever, thus enhancing generalization.
``W2. ESM2 performance reported in SaProt for contact prediction is higher.``
They used the 33-layer ESM2-33t model, while we opted for the 30-layer ESM2-30t model to ensure a fair comparison with previous knowledge graph-based models, which used a 30-layer ProtBert as the backbone. Despite having fewer parameters and layers than ESM2-33t, our model outperforms ESM2-33t on the short-term Contact task (Table 3), and achieves comparable performance on the ProteinGYM benchmark, as shown in Table 1.
``W3. Claims require further evidence. (1) The knowledge retriever enhances generalization to unseen proteins. (2) Kara mitigates catastrophic forgetting through unified knowledge integration.``
(1) As stated in Appendix B (Lines 637–639), we removed all proteins appearing in the downstream task datasets from the protein knowledge graph. Consequently, during inference, all proteins in the downstream tasks were unseen during training, and no related knowledge existed in the knowledge graph. Therefore, all results presented in the original paper reflect the model's performance on unseen proteins.
Additionally, Table 4 presents the model’s performance when the retriever is removed during fine-tuning and inference. The results show a substantial performance drop in the absence of the retriever, further highlighting its critical role in enhancing generalization.
(2) Due to space limitations, please refer to Reviewer pk6Q-W1.
``Q1. How well does Kara generalize to large-scale PKGs.``
As discussed in lines 263–274 on page 5, we designed the relation-GO combinations strategy to generalize to large-scale KGs. Table 6 presents the time cost with and without the retriever. The results show that, after applying this strategy, Kara's training and inference time only slightly increases compared to knowledge-free baselines (even on large-scale ProteinKG 65), demonstrating its scalability.
``Q2. How does retrieval noise or incomplete PKG affect the model.``
Table 8 in the original paper already analyzes the performance of different models when dealing with incomplete knowledge graphs.
Table 7 presents the performance when varying levels of noise are introduced into the retrieved results (by replacing retrieved knowledge with random knowledge). The results indicate that retrieval noise does not significantly impact performance. This is because the model's fine-tuning process does not rely on ground-truth knowledge and is inherently noisy, enhancing the model's robustness.
``Q3. Can retrieval be extended to handle proteins with missing knowledge?``
Our retriever is inherently designed to handle unseen proteins without relevant prior knowledge. It achieves this by predicting the most likely knowledge description for an unseen protein, linking it to the KG, and retrieving relevant structure as knowledge information. Therefore, regardless of whether a protein has associated knowledge or useful GO entities, the retriever can still process it. While prediction errors may occur, the impact of retrieval noise on model performance due to such errors has already been discussed in Q2.
``Q4. Is there a trade-off between retrieval depth and performance? Could a confidence-based retrieval mechanism improve accuracy?``
We propose a relation-GO combinations strategy, which balances the breadth and performance of retrieval by identifying the interacting entities specific to each relation. Moreover, the retrieval method does not require deep-first graph search, making it scalable for large KGs, as discussed in response to Q1. The performance of using the confidence threshold is provided in Table 8, showcasing a slight performance improvement.
``Q5. Why explicitly using knowledge (as of Kara) is better than the one encoded in pretraining?``
First, previous works have demonstrated that encoding knowledge directly into parameters can not accurately retain the knowledge information [1]. Second, KGs are subject to updates. Models based on parameter encoding cannot easily adapt to such updates and require retraining. In contrast, Kara explicitly integrates knowledge through virtual tokens, enabling it to seamlessly adapt to updates in the knowledge graph.
[1] Large language models struggle to learn long-tail knowledge. ICML 2023
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Rebuttal Comment 1.1:
Comment: Thank you for your clarification and update.
I keep my positive recommendation. Good luck. | null | null | null | null | null | null |
Optimal Fair Learning Robust to Adversarial Distribution Shift | Accept (poster) | Summary: This paper demonstrates that randomized fairness-aware classifiers have the local Lipschitz property, which makes them (somewhat) robust to adversarial perturbations of their training data. The authors demonstrate that randomization is crucial for this property (confirming a previously known result), but also demonstrate that it may be confined to a single point; finally, they bound the Lipshitz constant for several popular fairness criteria.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: There are no experiments in this paper.
Theoretical Claims: Yes; I did not find any issues.
Experimental Designs Or Analyses: There were no experiments.
Supplementary Material: I read the appendix.
Relation To Broader Scientific Literature: The key contributions present some properties of randomized fairness-aware classifiers that, as far as I know, are novel. As such, this work adds to the literature that studies randomized fairness-aware classifiers and demonstrates their advantages over deterministic ones in cases of fairness thresholds.
Essential References Not Discussed: None, to my knowledge.
Other Strengths And Weaknesses: I really appreciated the mostly clear writing of the paper and the intuitions provided. The authors’ positioning of their work in a sociological context by discussing the advantages and disadvantages of randomized classifiers vis-a-vis the sociological goals was also very nice.
Other Comments Or Suggestions: The intuition in Section 1.2. was not immediately very clear, it would have been helpful to have more explanation for how the 1-skeleton of the intersection of the hyperplane and the hypercube relates to the classifier and the datapoints.
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful feedback and for appreciating the novelty of our results and the clarity of presentation. We recognize the importance of making the intuition in Section 1.2 as clear as possible for better readability of the rest of our paper. Acting on your suggestion, we will update our manuscript with a diagram (similar to the visualization here https://cococubed.com/images/raybox/five_shapes.pdf).
We provide a brief verbal explanation here: The hypercube represents the space of all classifiers, with each dimension corresponding to a data point. The fairness constraint is modeled as a hyperplane. The intersection of any hyperplane with the hypercube results in a bounded region whose vertices are either (i) vertices of the hypercube itself or (ii) points formed by the intersection of the hyperplane with an edge of the hypercube. In other words, all vertices of this intersection lie on the 1-skeleton (or polytope graph) of the hypercube. Accuracy can be understood as a directional objective, and the fair BOC corresponds to an extremal point in that direction on the intersection of the hyperplane and the hypercube. Since, in every direction, an extremal point must be a vertex, and all vertices lie on the 1-skeleton, it follows that the fair BOC necessarily lies on the 1-skeleton of the hypercube.
We hope that our response adequately addresses your questions, and we sincerely request your support towards a consensus for acceptance of our paper.
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Rebuttal Comment 1.1:
Comment: I thank the authors for the additional context. I will keep my original rating for this paper. While I wouldn't call this work groundbreaking, I think that it's a solid contribution in terms of the new results that it contributes regarding adversarial robustness, as well as providing a nice and helpful intuition for fair classifiers and the role that randomization plays. | Summary: This paper analyzes/bounds the robustness of the optimal fair classifier $f$ (w.r.t. a distribution $\mathcal P$) under distribution shifts in terms of both accuracy and performance. The specific setting considered is binary class, binary group, in the attribute-aware setting, and the fairness criteria considered are SP, EO, EOpp (can be extended to other similar metrics).
In other words, what would the increase in the accuracy and unfairness of $f$ be if we evaluate it on $\mathcal P' \neq\mathcal P$?
Claims And Evidence: Yes
Methods And Evaluation Criteria: N/A
Theoretical Claims: Proofs are not checked, but the theorem statement/results are reasonable.
Experimental Designs Or Analyses: N/A
Supplementary Material: Did not review supplementary material.
Relation To Broader Scientific Literature: This paper considers the robustness of fair classifiers subject to distributional shifts; the exact contribution is the bound/sensitivity analysis for accuracy and unfairness of an optimal fair classifier evaluated on a shifted distribution.
But the reviewer is aware of similar results in prior publications that appear to subsume the results in this paper: see "Other Strengths And Weaknesses"
Essential References Not Discussed: See Other Strengths And Weaknesses.
Other Strengths And Weaknesses: Weaknesses.
While the results are concrete and rigorously established, the reviewer would like the authors to comment on the similarities/differences between these results and the sensitivity analysis in prior work for optimal fair classifiers:
- [Xian & Zhao, 2024]: Theorem 3.1 in Section 3.2 Sensitivity Analysis bounds the accuracy and unfairness of a classifier that is optimal and fair under a different distribution (specified via $\hat r\neq r$ for a shift in the label distribution, and $\hat g\neq g$ for a shift in the group membership distribution); this analysis applies to SP, EO and EOpp under attribute-blind setting for multigroup and multiclass classification, which is more general than the setting considered in this paper. They also seem to show that their bound has a matching lower bound by an example.
- [Chen et al., 2024]: Section E contains a similar sensitivity analysis, for the same setting except binary group and binary class.
- [Chen et al., 2022]: They also consider fairness under distribution shift, with a similar result that involves a Lipschitz condition. Could the authors comment on any similarities/differences between the two works?
[Xian & Zhao, 2024] A Unified Post-Processing Framework for Group Fairness in Classification
[Chen et al., 2024] Post-hoc Bias Scoring Is Optimal For Fair Classification
[Chen et al., 2022] Fairness Transferability Subject to Bounded Distribution Shift
Other Comments Or Suggestions: N/A
Questions For Authors: See Other Strengths And Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your time and insightful feedback. We will cite and discuss the novel results in the papers you pointed out. However, our results are incomporable to those of the papers mentioned. Fundamentally, the underlying settings are different, and these results complement each other.
**1. Comparison with [Xian & Zhao, 2024]:**
Significantly, our setup assumes $P_X$ is a *discrete* distribution (over either a discrete or continuous domain $X$), and we will make this explicit in our revision (note that this is a standard assumption for realistic tabular datasets with features like height, income, race, etc.). On the other hand, [Xian & Zhao, 2024] implicitly assume $X$ is a *continuous* domain, and their results in general hold only for continuous distributions $P_X$ over $X$. See Remark 2.4 (fail cases of Assumption 2.2) in [Xian & Zhao, 2024], where the results don’t hold when the push-forward distribution $r\#P_X$ contains atoms and the randomized Fair BOC splits their mass, corresponding to the case our paper deals with, i.e., discrete distributions (See Claim 1 in our paper).
There exist many examples of discrete distributions where the optimal fair classifier must be randomized, and resorting to a deterministic classifier must necessarily come with a sharp drop in accuracy (even with the perturbation step described in Proposition 2.3 of [Xian & Zhao, 2024]); see the example in Claim 1 in our paper, where perturbing the scores/risks of each point would not do away with the need for randomization. The technical challenges in the discrete setup are very different from those in the continuous setup. For example, in most discrete distributions, the optimal fair classifier must be randomized, whereas in continuous distributions a deterministic classifier suffices under Assumption 2.2 in [Xian & Zhao, 2024]. Unlike the continuous setting, enforcing determinism in the discrete setting typically leads to non-robustness, for example in Claim 1.
We also note that the approach mentioned in Remark 2.4 of [Xian & Zhao, 2024] to handle discrete distributions, i.e., smoothing the discrete distribution and then applying the algorithm in the paper with a deterministic classifier, does not apply to discrete domains; furthermore, for continuous domains it will almost certainly lead to a drop in accuracy.
To summarize, while our submission and [Xian & Zhao, 2024] share the focus on robustness and fairness, our respective underlying frameworks are fundamentally different and complementary.
Finally, we emphasize that our robustness guarantees (Theorems 1, 2, & 3) cover adversarial distribution shifts over $X\times Z \times Y$, whereas the sensitivity analysis in Theorem 3.1 of [Xian & Zhao, 2024] covers either a shift in label distribution over $X\times Y$, or a shift in group distribution over $X \times Z$.
**2. Comparison with [Chen et al., 2024]:** Unlike us, they do not deal with adversarial distributions shifts, but only label distribution shifts and/or group distribution shifts. In addition, our setups are fundamentally different, theirs being the continuous case, and ours being the discrete case. Moreover, their sensitivity analysis in Theorem 2 is looser, and has an extra additive error term, unlike ours and that of [Xian & Zhao, 2024]. Besides, they do not deal with the case of perfect fairness, and require $\delta > 0$.
**3. Comparison with [Chen et al., 2022]:** Their result is fundamentally different, and essentially shows that the fairness of a fixed hypothesis class on two similar distributions is similar. This is essentially what we show in Claims 2/5/6, however, they only deal with label and covariate shifts, while we tackle the more general case of adversarial distribution shifts.
We hope that our response has addressed your concerns, and if so, we respectfully request you to consider increasing your rating.
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Rebuttal Comment 1.1:
Comment: The reviewer would like to thank the authors for the response.
Regarding point 1 [Xian & Zhao, 2024]:
- The reviewer would like to point out that although their proposed algorithm requires the continuity assumption, their sensitivity analysis in theorem 3.1 does not... in fact, the result covers arbitrary distributions, discrete, continuous, or mixed, whereas the present work is only discrete. There is also this difference in generality that their result handles attribute-blind, multi-class, and multi-group, whereas the present only attribute-aware, binary class, and binary group. This, in reviewer's opinion, remains a major weakness...
- Although now irrelevant, the reviewer would like to point out that the smoothing technique used in theirs incur arbitrarily small drop in performance (see their discussions in section 2.2)
- The reviewer agrees with the authors that their theorem 3.1 only handles label shift and not covariate shift. Although, in the reviewer's humble opinion, an extension to handle covariate shift should be straightforward...
The reviewer's main concern regarding the limitation in the settings covered by the results in present work still holds, and as such, would like to keep the current rating—but considering that there is some novelty in handling covariate shifts, the reviewer would not be upset if the paper is accepted. In either case, the reviewer encourages the author to discuss and include these comparisons to prior work in the revision.
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Reply to Comment 1.1.1:
Comment: Thank you for reading our rebuttal and several thoughtful comments regarding comparison with the recent, unpublished work of [Xian-Zhao 24] (arxiv, 23 Dec 2024). We will definitely cite and discuss their work, and also explain why our results are not subsumed by [Xian-Zhao 24]. We highlight some strong points of our results below.
1. **Adversarial distribution shifts:** The sensitivity analysis (Theorem 3.1) in [Xian-Zhao 24] only holds for label *or* group shifts, whereas our robustness guarantee works for ***adversarial*** distribution shifts. *Adversarial* or arbitrary distribution shifts are strictly more general than label/covariate shifts, and moreover, they cannot be simulated by any combination of label/covariate shifts.
1. **Tighter analysis:** In the sensitivity analysis (Theorem 3.1, 2nd result) in [Xian-Zhao 24], the change in accuracy due to group distribution shift, is a constant in the case of perfect fairness (i.e., $\alpha = 0$). Then the expression $\min\left(1 - \alpha, \frac{\epsilon_g}{\alpha + \epsilon_g}\right)$ evaluates to $1$, so the excess risk is an additive $2||r||_{\infty}$, which is a constant independent of the amount of distribution shift. We prove a stronger Lipschitzness guarantee, where the excess risk goes to $0$ as distance between the distributions becomes arbitrarily small.
4. **Characterization and minimal randomness:** Theorem 2.1, and the perturbation/smoothing algorithm in [Xian-Zhao 24] does not hold for discrete domains. While the LP can be used to compute a randomized optimal classifier for discrete domains, there is no description of this classifier. On the other hand, we provide a complete characterization of the same, and show the existence of a *nearly-deterministic* optimal solution with minimal randomness, whereas in [Xian-Zhao 24], the optimal solution of the LP could use an arbitrary amount of randomization.
5. **Complexity:** Our algorithm is very simple and efficient, running in $O(|X| \log (|X|))$, while the algorithm in [Xian-Zhao 24] solves a large linear program with $O(|X|)$ constraints in $O(|X|)$ variables, requiring a much higher complexity.
3. **Multiple sensitive groups:** We recognize that [Xian-Zhao 24] applies to attribute-blind, multi-class, multi-group fair classification. Our algorithm and robustness guarantee can also be extended to the case of multiple sensitive groups, as stated in our Footnote 1 (page 3).
6. **Cost-sensitive risk:** As stated in our Footnote 2 (page 3), in addition to the standard $0$-$1$ loss $\ell_{0-1}$, our results also hold for the more general loss function $\ell_{\alpha}$ known as *cost-sensitive risk* [Menon-Williamson, 2018] that assigns weight $\alpha$ to False Positives and weight $(1-\alpha)$ to False Negatives.
- Menon, A. K. and Williamson, R. C., The cost of fairness in binary classification, FAccT 2018. | Summary: The paper studies the fairness-aware classification problem, where the goal is to maximize accuracy subject to the demographic parity or equal opportunity fairness constraint. The paper first discusses Claim 1 that a deterministic classification rule can have high sensitivity to perturbations to the data distribution. An example is discussed under Claim 1 to support this claim. Next, the discussion focuses on evaluating the sensitivity of the randomized fair classifier and the main result in Theorem 1 (and Corollary 1) shows an $\epsilon$ TV-perturbation to the data distribution leads to a worst-case $\epsilon$-times-a sensitive attribute probability constant difference in the accuracy of the optimal fair classifier.
Claims And Evidence: Only partially. My main concern with this submission is that the authors do not present any numerical and enough theoretical evidence that their theoretical claims are relevant to real non-synthetic data distributions. As I said, the paper does not provide any numerical evaluation of the claim that "deterministic fair classifiers are sensitive to adversarial noise".
Concerning the theory results, I think Claim 1 gives a rather degenerate setting where the deterministic fair classifier is sensitive to noise. The example discussed in the proof of Claim 1 focuses on a Binary input $X$, and from the construction of the example, it seems to me that the case is degenerate and highly depends on a binary input $x$ that is independent of the sensitive attribute variable $Z$ and then perturbed to exhibit correlation with the sensitive attribute $Z$.
I am wondering if such an example would be the case for a standard fairness-aware classification setting, such as COMPAS and Adult data. A significant difference in those real-world examples is that the input variable $X$ is multi-dimensional and the cardinality of possible input vector $x$ is much greater than the binary setting in Claim 1. Therefore, I am highly unsure if the issue highlighted in Claim 1 would be relevant to actual fairness-aware tasks. I believe the paper should provide enough evidence that this issue is more significant than a degenerate scenario, particularly because the entire paper is dedicated to showing the issue exists in the deterministic case, while it is not the case with randomized classifiers.
Methods And Evaluation Criteria: The paper has no numerical experiments on fairness-aware classification. Regarding the evaluation criteria in the analysis, the paper is missing the discussion of approximately fair classifiers. In practice, the demographic parity condition is not fully enforced in the classification, and instead a dependence quantity, such as mutual information or correlation metric, is regularized in the fairness-aware learning process. Therefore, the independence condition in DP does not strictly hold in real-world applications.
Studying the paper's main results and argument, it seems to me that the Binary-input $X$ example in Claim 1 can be easily addressed by relaxing the DP constraint to a bounded mutual information or maximal correlation. As said above, this has not been discussed in the paper.
Theoretical Claims: The main text includes the proof of Claim 1 and Theorem 1, and I think the theorems are correct. Still, I was wondering if the proof of Theorem 1 could have been shorter. On another note, I was wondering why the authors use about 3 pages to prove Theorem 1 before stating the result. I suggest discussing the theorem right after Claim 1 and postponing the proof to the supplementary material. The saved space can be used for numerical evaluation of the results and further theoretical discussion.
Experimental Designs Or Analyses: The paper presents no experimental results on fairness-aware classification.
Supplementary Material: Not in detail, I read the theorems on NP-completeness of deterministic fair classifier and the extension of the results to equal opportunity and predictive equality.
Relation To Broader Scientific Literature: I think the literature review and paper's discussion is missing a large body of related works on approximate fairness in fairness-aware classification. This includes references suggesting to replace the hard demographic parity constraint with regularizing dependence measures such as mutual information, Pearson correlation, HGR correlation, $f$-mutual information, and its special cases. In practice, the demographic parity and equal opportunity are not enforced with hard constraints, and instead there is an optimization constraint or regularization penalty term to penalize significant values of dependence between the variables. I understand that the paper focuses on the extreme case of completely fair classifier, but the discussion should still include some clues on how the results would theoretically or empirically relate to more practical scenarios.
Essential References Not Discussed: Please see my answer to the above question.
Other Strengths And Weaknesses: Please see my previous answers.
Other Comments Or Suggestions: Please see my previous answers.
Questions For Authors: 1- Can the authors provide standard fairness-aware classification settings (like COMPAS and Adult) where the observation in Claim 1 would be relevant?
2- Why the example in the proof of Claim 1 can hold in non-degenerate scenarios where the space of variable $X$ can include a large number of outcomes?
3- Can the proof of Theorem 1 be shortened and is Lemma 1 necessary to prove the lemma?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your time and insightful feedback. We respond to your comments below.
**1. Real-world datasets:** Our setup assumes a distribution over a discrete domain space $X$, which is a standard assumption for real-world tabular datasets (e.g., COMPAS) with features such as age, race, DoB, prior counts etc. We do not make any other assumptions on $X$. In particular, $X$ could be large, and multidimensional. The same holds for the non-robustness phenomenon is Claim 1. While experiments could be insightful, we emphasise that the focus of our paper is to establish the theoretical foundations of robust fair learning, building upon the theoretical papers of Konstantinov-Lampert (2022), and Blum et al. (2024).
**2. Larger, non-degenerate example:** In Claim 1, we provided a small example, independent of the sensitive attribute, just to demonstrate the phenomenon of non-robustness that occurs in optimal fair *deterministic* classifiers. The example can be made much larger (in fact, it can be made arbitrarily large). In addition, $X$ can also be multidimensional, and can depend on the sensitive attribute. The below example assumes $|X| = 10$, with $X$ also depending on the sensitive attribute. Consider the following distribution $P$.
$P,S(x_1, A) = (0.055, 0.9)$ | $P, S(x_1, D) = (0.045, 0.91)$ |
$P, S(x_2, A) = (0.055, 0.8)$ | $P, S(x_2, D) = (0.05, 0.78)$ |
$P, S(x_3, A) = (0.045, 0.73)$ | $P, S(x_3, D) = (0.045, 0.71)$ |
$P, S(x_4, A) = (0.04, 0.67)$ | $P, S(x_4, D) = (0.06, 0.63)$ |
$P, S(x_5, A) = (0.055, 0.53)$ | $P, S(x_5, D) = (0.05, 0.51)$ |
$P, S(x_6, A) = (0.045, 0.45)$ | $P, S(x_6, D) = (0.05, 0.46)$ |
$P, S(x_7, A) = (0.055, 0.33)$ | $P, S(x_7, D) = (0.06, 0.32)$ |
$P, S(x_8, A) = (0.04, 0.28)$ | $P, S(x_8, D) = (0.04, 0.24)$ |
$P, S(x_9, A) = (0.06, 0.17)$ | $P, S(x_9, D) = (0.055, 0.15)$ |
$P,S(x_{10}, A) = (0.05, 0.09)$ | $P, S(x_{10}, D) = (0.045, 0.7)$
Consider $f$, which classifies $\{x_1,..., x_5\} \times \{A, D\}$ as $1$, and $\{x_6,...,x_{10}\} \times \{A, D\}$ as $0$. $f$ satisfies $DP$, and has accuracy much more than $0.5$. Consider the neighboring $P^′$ which differs with $P$ on $(x_5, A)$, and $(x_5, D)$, as follows.
$P', S(x_5, A) = (0.055 + \epsilon, 0.53)$ | $P', S(x_5, D) = (0.05 - \epsilon, 0.51)$,
where $\epsilon > 0$ is arbitrarily small. There are only 2 deterministic classifiers satisfying DP on $P’$, either the constant 1 classifier $f_1$, or the constant 0 classifier $f_0$, both with accuracy close to 0.5. Hence, the difference in accuracy of the deterministic DP-fair BOC on arbitrarily close $P, P^′$ is large, demonstrating non-robustness.
**3. Proof length:** Perhaps the proof can be shortened, we will try and simplify it to aid readability. Lemma 1 played a crucial role in simplifying the proof overall, but it can be done without Lemma 1 as well.
**4. Approximate fairness:** We show through the example below that the non-robustness phenomenon highlighted in Claim 1 also holds when we only require approximate fairness. In particular, this can hold in the case where sensitive group populations are highly imbalanced, for example when the mass of group $A$ is much larger than the mass of group $D$, i.e., $P(A) >> P(D)$. We define a $\delta$-approximately fair classifier as follows, “If $r$ denotes selection rate, a classifier $f$ is $\delta$-approximately DP-fair if $|r(f, A)−r(f, D)| < \delta$". We set $\delta=0.25$, and slightly modify the example in Claim 1, where we skew the probability mass towards Group $A$ (in Claim 1, the group masses are balanced). Consider a distribution P, where
$P, S(x_1, A) = (0.4, 1)$ | $P, S(x_1, D) = (0.1, 1)$ |
$P, S(x_2, A) = (0.4, 0)$ | $P, S(x_2, D) = (0.1, 0)$
Consider the (deterministic) classifier $f$, with $f(x_1, A) = f(x_1, D) = 1, f (x_2, A) = f (x_2, D) = 0$. $f$ satisfies DP, and $\text{Acc}(f) = 1$. Consider the neighboring distribution $P^′$ differing only on $(x_1, D), (x_2, D)$, as follows.
$P', S(x_1, D) = (0.1 + 0.05, 1)$ | $P', S(x_2, D) = (0.1 - 0.05, 0)$
If we apply $f$ on $P’$, it does not satisfy approximate DP for any $\delta < 0.25$, even though $TV(P, P’)$ is small ($0.05$). There are only 2 deterministic classifiers satisfying approximate DP for any $\delta < 0.25$, either the constant 1 classifier $f_1$, or the constant 0 classifier $f_0$, with $\text{Acc}(f_1) = 1/2 + 0.05$, and $\text{Acc}(f_0) = 1/2 − 0.05$. Hence, the difference in accuracy of the deterministic (approximate) DP-fair BOC on closeby $P, P^′$ is almost 0.5, demonstrating non-robustness.
We will also discuss fairness regularizers based on mutual information, Pearson correlation, HGR correlation, and f-mutual information. These are relevant for broader literature review but not directly related to the problem we study.
We hope we have addressed all your concerns, and we sincerely request you to reconsider our rating.
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Rebuttal Comment 1.1:
Comment: I thank the authors for their responses to my comments. I appreciate theoretical contributions to the machine learning literature, and I found the discussion comparing randomized and deterministic classification rules in the paper to be interesting.
However, I am still unconvinced that the issues raised in the paper have significant implications for real-world applications of fairness-aware classification. I would appreciate the authors' further clarification on the following points:
1. Can the authors provide any numerical evidence using real datasets where the theoretical discussion described in the paper leads to any demonstrable form of lack of robustness in deterministic fairness-aware classification rules? There is no such numerical evidence in the paper or the authors' response.
2. Is there a general class of distributions on $X \times Y \times Z$ under which the robustness issue for deterministic fairness-aware classification rules provably holds? The arguments in the paper and the authors' response are based on specific, constructed examples, making it difficult to see the actual severity of the robustness issue.
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Reply to Comment 1.1.1:
Comment: Thank you for reading our rebuttal and your insightful comments on our responses. We respond to your questions below.
1. **Robustness of fair classifiers on real-world data:** Robustness of fair classifiers under bias/shift in the data distribution is a well-known issue in fair machine learning literature. Akpinar et al. (https://arxiv.org/pdf/2204.10233) empirically study the robustness of BOC and fair BOC on synthetic data distributions and provide a sandbox tool for stress-testing fair classifiers. Sharma et al. (https://arxiv.org/pdf/2302.05906) and Ghosh et al. (https://arxiv.org/pdf/2307.03306) empirically study robustness of fair classifiers under data bias on semi-synthetic real-world datasets (i.e., real-world datasets with synthetically injected bias/shift). In both these papers, Exponentiated Gradient Reduction (EGR) or ExpGrad (https://arxiv.org/pdf/1803.02453) stands out for its better robustness under data bias/shift, and it is inherently a randomized classifier. We can discuss these works, if you think it is not a digression from our main result. However, reconciling our theoretical results with empirical observations on real-world datasets is an important direction for future work, but not the focus of this paper.
1. **General class of distributions:** Apart from the empirical evidence in the above papers, here is a uncountably infinite general class of distributions on which we can *provably* show non-robustness of deterministic fairness-aware classifiers. Consider a domain set as $(x_1, x_2, … x_n)$$\times$$(A,D)$, where $n$ is an arbitrary positive integer. Now, for each point $(x_i, z)$ in the domain (where $z \in (A,D)$), choose its probability mass and score to be random number from the uniform distribution over $[0,1]$ (or any continuous distribution over $[0,1]$). Make sure this forms a probability distribution by normalizing the probability masses suitably. Sort the points in each group by score, and choose $i, j$ i.i.d. from $(1, …, n-1)$. We now want the boundaries of the first $i$ elements of $A$, and first $j$ elements of $D$ to align. Choose $r$ from the uniform distribution over $[0,1]$ (or any continuous distribution over $[0,1]$), and normalise suitably so that the first $i(j)$ elements of group $A(D)$ comprises of $r$ fraction of the total mass of that group. Call this transformed distribution $P$. Now, randomly perturb the score/mass of each element by a small amount (for example, from the uniform distribution over $[0, \epsilon]$, for small $\epsilon > 0$), and call this neighbouring distribution $P’$. For distribution $P$, the (deterministic) classifier that accepts the first $i$ elements of $A$, and first $j$ elements of $D$, and rejects the others, satisfies DP, and is significantly more accurate than the constant $0$ and constant $1$ classifier. Also, it is easy to see that (almost surely) none of the boundaries will align for $P’$. Hence, the only (deterministic) classifiers satisfying DP on $P’$ are the constant $0$ and constant $1$ classifiers, resulting in a significant drop in accuracy, and demonstrating non-robustness. | Summary: The authors study the robustness of the Fair Fair Bayes Optimal Classifier (BOC) to adversarial noise in the data distribution. They show that the robustness guarantee for BOC breaks down when fairness constraints are aded and propose a randomized Fair BOC that is robust to malicious noise in the data distribution. They demonstrate this with various fairness constraints such as Demographic Parity, Equal Opportunity and Predictive Equality.
Claims And Evidence: The proofs for the theoretical claims are thorough. I would like to see additional empirical results as well to solidify the claims.
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes, I reviewed the proofs and claims but it is possible that I missed something.
Experimental Designs Or Analyses: There is no direct experimental design. An empirical analysis is missing.
Supplementary Material: Yes, it was very thorough.
Relation To Broader Scientific Literature: Yes, fairness issues have grown in importance and ensuring that adding fairness constraints preserves robustness is an important contribution.
Essential References Not Discussed: Not that I noticed.
Other Strengths And Weaknesses: The motivation and the writing are very clear and easy to follow. The theoretical contributions and proofs are also clear.
Other Comments Or Suggestions: I would suggest validating the contributions with empirical results as this would make the paper stronger.
Questions For Authors: While the randomized Fair BOC is shown to be nearly deterministic, the existence of stochasticity may limit it's applicability over BOC. Is this a concern?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your insightful feedback, and for appreciating the importance of our contribution, and the clarity of presentation. We respond to your comments below.
**1. Experiments:** We emphasise that the focus of our paper is to advance the theoretical foundations of robust fair learning, building upon the theoretical works of Konstantinov-Lampert (2022) and Blum et al. (2024). While experiments would be valuable, we leave that as future work.
**2. Randomization:** It is established that on most distributions, (exact) fairness is non-trivially achievable only by randomized classifiers [Agarwal et al, Hardt et al.]. In addition, the randomization in our result is almost nil, and is the minimum amount required (only on one element). If we strictly enforce determinism, the drop in accuracy is significant, as demonstrated in Claim 1. Hence, there is a clear tradeoff between randomization and accuracy (subject to fairness), and for a tiny amount of randomness, we obtain a big jump in accuracy.
1. Moritz Hardt, Eric Price, and Nathan Srebro. Equality of Opportunity in Supervised Learning. NeurIPS 2016
2. Alekh Agarwal, Alina Beygelzimer, Miroslav Dudík, John Langford, and Hanna Wallach. A Reductions Approach to Fair Classification, ICML 2018.
We hope that our response has addressed your concerns, and if so, kindly request you to consider increasing your score, and support towards a consensus for acceptance of our paper.
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Rebuttal Comment 1.1:
Comment: I confirm that I have read the author response. I maintain my score. I still feel that the addition of experimental results to validate the theoretical contributions are needed to increase the impact of the paper. I am still recommending a weak accept as the theoretical contributions are strong and useful.
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Reply to Comment 1.1.1:
Comment: **Empirical validation:** Below we discuss some recent works that empirically study robustness of fair classifiers under data bias/shift and explain the limitations and challenges in doing similar empirical validations for our paper. Akpinar et al. (https://arxiv.org/pdf/2204.10233) study robustness of Bayes Optimal Classifier (BOC) and fair BOC on synthetic data distributions by injecting bias/shift in a stylized set-up. They use a simple Gaussian data distribution (Subsection 4.2 (1) in their paper), so that BOC and fair BOC are linear because these classifiers are NP-hard to compute on general distributions. Sharma et al. (https://arxiv.org/pdf/2302.05906) and Ghosh et al. (https://arxiv.org/pdf/2307.03306) study robustness of fair classifiers under injected data bias/shift on semi-synthetic data (i.e., real-world datasets with synthetically injected bias/shift). Both these papers observe that the Exponentiated Gradient Reduction (EGR) or ExpGrad (https://arxiv.org/pdf/1803.02453) stands out for better robustness under data bias/shift, and it is a randomized classifier by construction (i.e., a random ensemble of classifiers). Our work studies deterministic-vs-randomized BOC and fair BOC under a more general *adversarial* data bias/shift that is much harder to construct empirically on real-world data. As you mentioned, reconciling our theoretical results with empirical observations on real-world datasets is important. However, we consider it as independent future work and cannot address it here given the focus of our current paper and limited time. We greatly appreciate your constructive criticism nevertheless. | null | null | null | null | null | null |
Tokenized Bandit for LLM Decoding and Alignment | Accept (poster) | Summary: The paper "Tokenized Bandit for LLM Decoding and Alignment" introduces a novel Tokenized Bandit (TB) framework to address LLM decoding and alignment challenges. It models LLM decoding as a sequential decision-making problem, using multi-armed bandit (MAB) and linear bandit (LB) techniques to optimize token selection.
Claims And Evidence: The DDMC assumption is not universally validated. It is tested on limited datasets, and it's unclear whether it holds for other LLM applications (e.g., coding, mathematical reasoning).
Methods And Evaluation Criteria: Expanding evaluations to more datasets, and efficiency benchmarks (e.g., PPO, Best-of-N decoding) would significantly strengthen the paper’s claims.
Theoretical Claims: The regret bound relies on DDMC, but the paper does not rigorously prove whether DDMC always holds across different tasks.
And the proof assumes perfect token embeddings $e(x_t,y)$, but in reality, embeddings could introduce variance that affects regret analysis.
Experimental Designs Or Analyses: 1. While the paper claims that bandit-based decoding is superior, it does not compare against reinforcement learning approaches, which are common in LLM alignment. For example, Best-of-N Sampling and Direct Preference Optimization (DPO) are stronger baselines for alignment than standard greedy decoding.
2. I worry about the practical applicability of the approach: Tokenized Bandit selects tokens step by step but assigns rewards at the sequence level, making it hard to attribute rewards to individual tokens. Moreover, Bandit algorithms assume independent token selection, while **LLM generation has strong sequential dependencies**, raising doubts about their effectiveness in optimizing decoding. In practice, greedy decoding is rarely used due to repetitive outputs, possibly caused by the independence assumption in token selection.
Supplementary Material: without supplementary material submission
Relation To Broader Scientific Literature: The paper should expand the discussion on prior search-based decoding, RLHF baselines, and uncertainty-aware text generation to strengthen positioning in the broader literature.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Other Strengths:
1. The paper also introduces the Diminishing Distance with More Commons (DDMC) hypothesis, which states that if two sequences share the same suffix, their reward difference decreases. This assumption significantly reduces computational complexity and justifies the effectiveness of greedy decoding.
2. The paper theoretically proves that greedy decoding can be globally optimal under the DDMC hypothesis.
Other Weaknesses:
1. The paper assumes that the reward function 𝑢ₜ(𝑥ₜ, 𝑦) follows a linear structure: $𝑢ₜ(𝑥ₜ, 𝑦) = ⟨𝜃, 𝑒(𝑥ₜ, 𝑦)⟩$. However, in real-world LLM tasks, user preferences 𝑓(𝑥ₜ, 𝑦) may exhibit highly nonlinear behavior.
2. In the Tokenized Multi-Armed Bandit (TMAB) setting, the reward can only be observed after generating the entire sequence, making it difficult to directly determine the contribution of individual tokens. To address this, the authors adopt the Explore-Then-Commit (ETC) approach, estimating the utility of each token through multiple full-sequence samples. However, I am concerned that the number of required full sequences might be excessively large, potentially leading to a high computational cost.
Other Comments Or Suggestions: 1. I could not find the explicit formulation of the embedding function e(x_t, y). Does it lack an explicit expression? Or can you explain how to evaluate whether the token sequence y is suitable to query x_t, i.e., where is the reward r come from?
2. Regarding the definition of the utility function, could the authors provide some intuitive examples to justify its formulation? The current definition seems somewhat unconventional.
3. Concerning the experimental results, in the second figure, the convergence result appears to be around 20, which does not seem very satisfactory. I suspect that a significant factor contributing to this issue might be the formulation or definition of the utility function. Could the authors elaborate on whether any alternative formulations were considered?
4. Minor error: (1) In algorithm 2, there is a mistake in the selection of \tau^{\star}. (2)For y^{(i)}, it is the i-th token in sequence \bm{y}, but you use boldface on it, is it a typo?
Questions For Authors: 1. In the exploration phase of GreedyETC (Greedy Exploration-Then-Commit), how is the reward assigned to individual tokens when a full sequence must be generated before obtaining a reward? Since the reward is only observed at the sequence level, how do you estimate the contribution of each token during exploration?
2. The paper formulates LLM decoding as a Tokenized Bandit problem, where each token is selected sequentially, and the final reward is only observed after a complete sequence is generated. Given this delayed reward structure, how does the proposed bandit-based approach achieve global sequence-level optimization? Would a Combinatorial Bandit or Reinforcement Learning (RL) approach be more appropriate for handling dependencies between tokens?
3. It is unclear how a bandit approach, which is typically state-independent, can effectively guide token selection when the reward is assigned only after the entire token sequence $y_t$ is generated. Since token selection is not a set-based decision but rather a structured ordered sequence, different sequences lead to vastly different rewards, and the contribution of each token is not independently determinable. How does the bandit framework, which does not model dependencies between token choices, provide meaningful guidance in this setting?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We truly appreciate your insightful comments.
We will first make a general remark on our main contribution, answer major concerns and then remaining questions.
# General remark on main contribution / assumption
We kindly refer to our **response (General remark on main contribution) to Reviewer 3dxc**.
# Major concerns
## 1. Individual token reward
We note that individual tokens **do not** have any rewards, but only a token sequence does.
Our algorithm smartly learns an efficient path to the optimal sequence only by observing seqeunce-wise rewards, thanks to the novel DDMC assumption.
## 2. Sequential dependency
Our settings intrinsically **considers sequential dependency** given what has been chosen previously, since these histories are encoded in the sequence function’s value and also final embedding vectors.
Indeed, our offline benchmark selects a sequence with the largest utility that does account for the sequential dependency of the LLM, and the regret is computed with respect to this.
Thus, our goal is to learn efficient ‘sequence’ not individual token, and the previous decisions affect onwards.
We also remark that greedy decoding often provides repetitive outputs, especially for small language models few years ago, but this phenomenon is mitigated in the most recent LLMs (Song et al. 2024).
Practically, one can replace greedy decoding with other decoding schemes in EOFUL algorithm based on its empirical performance, which will be a great direction for future work.
## 3. Comparison with other benchmarks - PPO, DPO, Best of N
For PPO and DPO, we refer to **our response (Comparison to ARGS / PPO in RLHF) to Reviewer 3dxc**.
For the Best-of-N alignment, one could consider Best-of-N algorithm that knows the latent reward function in hindsight in our regret definition as an offline benchmark (note that this is **not an online learning**).
However, this will be weaker benchmark than offline greedy decoding under DDMC assumption.
Practically, one can replace the greedy decoding with best-of-n (or other decoding schemes) in EOFUL algorithm.
# Further comments
## 1. Perfect embeddings
Once the regret benchmark and a learning algorithm share the same embedding vector (even perturbed), all our theoretical results would naturally follow.
Also, standard LLMs operate based on the embedding vectors and corresponding logit probabilities, so the algorithm can naturally access embedding vectors, which is how we obtain embeddings in our evaluations.
## 2. State-dependency
Our contextual bandit framework captures state-dependency, and we hope our response (Sequential dependency) resolves your question.
## 3. Comments on DDMC with more datasets
We kindly refer to our response (More justification on DDMC) to Reviewer 3dxc.
## 4. Linear realizability assumption
We kindly refer to our response (Comments on linear realizability) to Reviewer amHn.
## 5. ETC approach in TMAB
Our study on TMAB is to provide more comprehensive theoretical findings for ‘tokenized’ variants of the bandit problems, whereas we believe our TLB setting is more practical for LLM applications.
That said, the fact that greedy ETC achieves the regret sublinear in $T$ and linear in the length of the sequence in TMAB implies that the number of samples required to learn efficient sequence is not significant.
We note that a naive algorithm requires exploring every possible sequence inducing regrets exponential in the length of the sequence.
## 6. Using combinatorial bandit or RL
As our objective function is a sequence function not a set function, standard combinatorial bandits can't be directly applied.
Further, one may generalize TLB to Markov decision process as does in RL, but this would be waymore complicated to analyze and it is not certain if it would exhibit Markovian property.
## 7. Explicit formulation of the embedding function
We hope our response (Perfect embedding) resolves your question.
Also, a noisy reward is observed after the LLM submits the entire outputs y, similar to the standard bandit framework, e.g., see L#146 (right column) on page 3.
## 8. Utility function
We hope our response (Linear realizability assumption) resolves your question.
Also, the weighted average of original LLM’s probability and another external reward module’s score is often considered for LLM alignment, e.g., see Khanov et al., 2024.
## 9. Convergence on the experiment results
Our interest is not on the convergence, but whether it exhibits a decreasing trend with respect to more common tokens as the definition of DDMC.
## 10. Minor error: (1) In algorithm 2, there is a mistake in the selection…
Thanks for catching - will edit it. Also yes, $y^{(i)}$ is $i$-th token (single token) - we abuse boldface to make it consistent with $y^{(i:j)}$ which is a sequence.
# References
* Song et al. 2024, The Good, The Bad, and The Greedy: Evaluation of LLMs Should Not Ignore Non-Determinism
* Khanov et al. 2024, Alignment as Reward-Guided Search
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Rebuttal Comment 1.1:
Comment: I’m not sure if I’ve missed something here. Due to space constraints, the author’s responses can’t be overly detailed, but I’d like the author to provide a clearer explanation: how do they address the issue of strong sequential dependencies? namely, how is the reward or feedback for the intermediate token selection process determined, since a reward is only obtained after generating an entire sentence? This problem is somewhat similar to the distinction in LLM reasoning between outcome and process reward models. Defining rewards for intermediate steps in a process reward model is notoriously tricky—here, that’s equivalent to assigning a reward for each token selection. Notably, this paper isn't relying on training; we’re just using a lightweight bandit approach. I still don’t fully grasp how the author resolves this challenge.
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Reply to Comment 1.1.1:
Comment: We sincerely appreciate the reviewer for detailed questions.
We will give an intuition behind how our algorithm and assumptions enable efficient learning without intermediate feedback, focusing on the TLB setting.
Note that the arguments for TMAB follow similar intuition, though details are different.
# Intuition off the top of one's head
In short, efficient learning is possible via (0) structural assumptions on DDMC and linearly realizable reward, (i) fact that offline greedy decoding is optimal under DDMC, (ii) we make an estimator $\tilde{\theta}_t$ for $\theta$ each round given feedbacks and use it for the decoding, (iii) the combination of LinUCB style of algorithm plus greedy decoding incurs only a small error for each token-wise decision compared to the offline greedy decision given that the estimator $\tilde{\theta}$ is not very far from $\theta$, and (iv) aggregating all these conclude efficient regrets bounds.
Notably, structural assumptions imposed on the sequence reward function by **DDMC assumption** and **linear utility function** with respect to embedding vectors enable us to efficiently decode tokens to find efficient sequence.
One may interpret the intermediate reward as the expected utility of the subsequence given estimators of the latent parameters.
Alternatively, rather than considering arbitrary reward function of the LLM, we show that if the utility (reward) satisfies reasonable structural assumptions, one can efficiently learn it in decoding time with online feedback.
Thus, our results may be also of interest to LLM reward modeling in handling the trade-off between deploying simple model versus efficiency.
EDIT: To clarify a bit more, in general situation, credit assignment is notoriously hard as the reviewer pointed out. But in online learning scenario, certain amount of errors are inevitable as we need to learn the latent parameters on the fly, and the objective is to have cumulative errors negligible w.r.t. number of samples (ideally sublinear in $T$) and this becomes possible as presented above.
# Overall arguments
Our overall arguments proceed as follows:
1. We prove that offline greedy (that knows the $\theta$) is optimal under DDMC.
2. Thus, our algorithm's objective boils down to mimic the offline greedy algorithm's behavior sample-efficiently.
3. Mainly, we combine the LinUCB style of algorithm with greedy decoding scheme that constructs an estimator $\tilde{\theta}_t$ and confidence ball $C_t$ using available history, and use it to decode at round $t$.
4. We prove that for every token decision above, the token-wise regret is sufficiently small as a function of the radius of $C_t$ and error of $\tilde{\theta}_t$.
5. Aggregating these error terms carefully with appropriate parameters, the regret can bounded by $L\sqrt{T \ln T}$.
We note that we slightly revise the arguments for sake of understanding, and is a bit different from the actual steps.
We refer to (L#289, page 6) below Theorem 3.8 and proofs for more details.
# Detailed explanation for each argument
1. Offline greedy is optimal under DDMC
First, we show that if we know the latent parameter $\theta$, greedy decoding is optimal under DDMC.
Here's a rough proof sketch.
Suppose not and say $o$ is an optimal sequence and $g$ is the sequence created by greedy decoding such that $u(o) > u(g)$.
Suppose $o$'s length is $L$.
If $L = 1$, then contradiction since $g$ makes myopically optimal decision.
Then, for induction argument we assume $g$ is optimal for $L-1$, and validate $L$.
This is done by comparing $o^{(1:L)}$ with a sequence $f$ that appends $o^{(L)}$ upon $g^{(1:L-1)}$ and utilizing DDMC assumption as well as the greedy decoding's nature.
2. Objective becomes mimicking greedy
Thus, if algorithms can make exact greedy choices for each token, then regret is zero.
On the other hand, since we don't know $\theta$, we need to learn it efficiently.
3. LinUCB + greedy decoding
- Once we have round $t-1$ feedback, we construct an estimate $\tilde{\theta}_t$ and confidence ball $C_t$.
- Then, for the next round $t$'s first token, we select the token that maximizes LinUCB index.
- This procedure is repeated for every token by appending the new token to the previously selected tokens and compute LinUCB index given corresponding embeddings.
- After it reaches EOS token, we submit and observe the feedback, and repeats.
4. Token-wise regret
Finally, total regret is decomposed by the summation of regrets over each round/token.
Fix a round $t$. For $l$-th token selection, by DDMC assumption, we relate the error made at $l$-th token selection to the error made at $l-1$-th token selection. Telescoping, the round $t$ regret can be written as a function of the error made at the first token selection, which can be written as the error rates of $\tilde{\theta}$ and the radius of $C_t$.
5. Aggregating round-wise regrets
Using algebraic arguments, we conclude that summing up these regrets overall induce sublinear regret. | Summary: The paper introduces two new bandit variants, the tokenized linear bandit (TLB) and tokenized multi-armed bandit (TMAB), which involve sequentially constructing a sequence of tokens to optimize a (random) utility function of a user, given a query. They introduce the DDMC assumption on token sequences and construct learning algorithms for both TLB and TMAB for which they prove regret bounds. They show that LLM alignment may be viewed as an application of their TLB method for specific functional forms of utility misalignment between the model and the user. They also aim to empirically validate the DDMC assumption in the context of LLMs and connect it to the empirically observed high performance of greedy decoding in LLMs.
## update after rebuttal
Following the author response, I am *provisionally* increasing my score to a 3, subject to discussion with the other reviewers.
Claims And Evidence: I have not been able to evaluate all the proofs, but claims seem generally well supported, with a few exceptions.
My first worry is regarding the suggestion that this method may be useful for alignment. It seems that the TLB problems only applies insofar as the linear realizability assumption holds, as well as the particular functional form of misalignment suggested in section 5.1. The paper contains no empirical verification of this in typical alignment settings.
My second worry relates to the DDMC assumption. The validity of the assumption is evaluated assuming the utility is parameterized to fit the form of distance functions d1 or d2 (sec 5.3), and in those cases it broadly (though not always, inspecting figure 1) seems to hold on Llama-3-8B-Instruct for the two datasets tested. However, this is not evaluated on more free form utility functions, such as those provided by human subjects or even reward models. In particular, it seems this assumption cannot hold in general (as shown in figure 1), and in particular it seems to omit some rather standard use cases of LLMs.
For instance, take the following token sequences:
q = "Suggest a cafe I should visit in Vancouver.",
y = "Visit Cafe Alice",
z = "Visit Cafe Bob",
\tau = "by"
y and z could plausibly be equal token length (this depends on the tokenizer, which is not part of the assumption). If 'Cafe Bobby' exists and 'Cafe Aliceby' does not exist, then utility z + tau is presumably larger than y + tau, even thought utility of y and z were presumably equal. Thus, the gap has increased.
In the case that u = p, the DDMC assumption implies that the difference in probability under the LLM of y and z is smaller than that of y + tau and z + tau, which seems unreasonable if 'Cafe Bobby' exist and 'Cafe Aliceby' does not, but 'Cafe Bob' and 'Cafe Alice' both exist. This suggests that p does not fit theorem 5.1, so the claimed connection to the success of greedy LLM decoding seems somewhat unreliable.
Note that this is dependent on the state of the world, which is not part of the assumption statement for obvious reasons, but without it the statement makes potentially unsupported assumptions about the world. The general issue is that tokens mean very different things in different contexts, so sharing more tokens does not guarantee that utilities are closer in many cases.
Methods And Evaluation Criteria: Testing the DDMC assumption with Llama-3-8B-Instruct on the TruthfulQA and HH-RLHF datasets is sensible. However, as mentioned above, the utility here is assumed to be parameterized in two very specific ways, and it would be instructive to see whether DDMC holds empirically with more free form utility functions, such as those provided by human subjects or even reward models.
Theoretical Claims: I have not been able to evaluate the proofs.
Experimental Designs Or Analyses: See previous fields.
Supplementary Material: I reviewd the related work section of the supplementary material, which seems sufficiently comprehensive.
Relation To Broader Scientific Literature: The paper proposes two new discrete bandit problems with applications to LLM decoding and alignment. I am unaware of earlier works on this intersection, but I am not too familiar with that literature. The paper aims to provide evidence towards a mechanism for the success of greedy decoding, which is a topic of current interest given the ubiquity of LLMs. For the same reason, results on decoding time alignment are relevant.
Essential References Not Discussed: Nothing particular that I am aware of. There is a wide literature on decoding time alignment that was not discussed (e.g., steering methods such as Panickssery et al. 2023, "Steering Llama 2 via Contrastive Activation Addition" and Todd et al. 2023, "Function Vectors in Large Language Models"), but it does not relate to the methods proposed in this work too directly.
Other Strengths And Weaknesses: Strengths:
- The paper is generally well written and structured.
- The paper contains many notes pointing to related work and exact implications of assumptions and statements. The authors seem very aware of the mathematical literature, although this is hard for me to reliably evaluate.
Weaknesses:
- Primarily the degree to which the assumptions (DDMC and to a lesser extent linear realizability of utility functions) hold in practice and the absence of (compelling) experimental evidence for these assumptions and the application of the work to alignment.
Other Comments Or Suggestions: Typo in proposition 3.3: "assumptinon"
Questions For Authors: 1. Under what conditions can we expect DDMC to hold, and is this realistic for typical LLM use cases?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We truly appreciate your detailed feedback and insightful comments.
We will first make a general remark on our main contribution, and then answer the reviewer’s comments/questions one by one.
# General remark on main contribution
We kindly ask the reviewer to see **our response (General remark on main contribution) to Reviewer 3dxc**.
# Comments on DDMC
We hope our general remark above partly resolves the reviewer’s concern regarding the necessity of the assumption.
As the reviewer pointed out, we don’t believe that DDMC would universally hold for every real-world scenario.
However, we empirically find an overall tendency to do so, i.e., having a decreasing utility difference (or decreasing distance between embedding vectors) as we append more common tokens.
Our DDMC assumption, or at least a relaxed version of it, is quite reasonable intuitively. For instance, in extreme cases, if we append a lot of common tokens in each of two sequences of the same length, one could expect that the user will realize a similar experience of reading them. Further, as we discussed in L#234, page 5, this shares similar intuition from the widely adopted submodularity on set functions.
Also, we conducted a few **more experiments** to cement our assumption’s effectiveness.
It can be found in https://anonymous.4open.science/r/temp-03AC.
In new experiments, we first tested DDMC assumption on two more datasets: AdvBench (standard jailbreak benchmark) and just-eval-instruct that contains many prompts of various tasks. Further, we verified DDMC assumptions beyond our linear utility function. We considered three more functions: L1/3/4 distance. In all these scenarios, we observe a tendency that appending more common tokens decreases the utility gaps. We will certainly add these experiments in the revision.
# Under what conditions can we expect DDMC to hold...
Thanks for a great question.
Although it’s difficult to classify certain characteristics of tasks that DDMC would more strongly hold, through our empirical verifications (including **newly added ones**), we have identified that in several commonly-used LLM alignment datasets, DDMC assumption seems to hold, so we believe this assumption is reasonably realistic (though certainly not universal).
# Comments on linear realizability
We hope our general remark above partly resolves the reviewer’s concern regarding the necessity of the assumption.
As we noted in our manuscript (paragraph below Assumption 3.2), several papers in the literature for LLM alignment often assume linear realizability for theoretical sake, e.g., we refer to Cen et al. 2024 and Yang et al. 2024 that exactly assume the linear realizability for theoretical purpose in LLMs
From practical perspectives, **several** recent empirical studies provide evidence that linear realizability is reasonable in many scenarios.
First, Zou et al. 2025 confirmed that concepts like truthfulness or ethics could be extracted via linear transformation over LLM’s representation (embedding) with fixed weights, which is also validated through extensive experiments.
Wang et al. 2024 tackled decoding-time alignment solely by using linear transformation over the LLM’s representation with carefully chosen weights to handle the harmlessness alignment.
Kong et al. 2024 considered a control theoretical perspective for LLM alignment by adding a linear perturbation on original logit vector.
Another relevant literature is the recently studied ‘linear representation hypothesis’, which gives a mechanistic interpretation on how LLMs embed concepts in representation space, as noted in our footnote 14.
In particular, the hypothesis itself states (as hinted by its name) that concepts / semantics (e.g., politic ideology, geography, and temporal knowledge) are embedded in a linear manner given some proper weights: we refer to Kim et al. 2025, Jiang et al. 2024, Park et al. 2025, Gurnee and Tegmark 2024 for more details.
Finally, we believe extending the linear function to nonlinear function in a similar vein to the extension of linear contextual bandit to nonlinear contextual bandit via kernelization by Valko et al. 2013 would be a great direction for future works.
# References
* Cen et al. 2024, Unified Approach to Online and Offline RLHF
* Yang et al. 2024, Asymptotics of Language Model Alignment.
* Zhou et al. 2025, Representation Engineering: A Top-Down Approach to AI Transparency
* Wang et al. 2024, InferAligner: Inference-Time Alignment for Harmlessness through Cross-Model Guidance
* Kong et al. 2024, Aligning Large Language Models with Representation Editing: A Control Perspective
* Kim et al. 2025, Linear Representations of Political Perspective Emerge in Large Language Models
* Jiang et al. 2024, On the Origins of Linear Representations in Large Language Models
* Park et al. 2025, The Geometry of Categorical and Hierarchical Concepts in Large Language Models
* Gurnee and Tegmark 2024, Language Models Represent Space and Time | Summary: The paper introduces the Tokenized Linear Bandit (TLB) and Tokenized Multi-Armed Bandit (TMAB), which are variants of the classical linear and stochastic multi-armed bandit problems, inspired by the decoding and alignment processes in large language models (LLMs). In these problems, a user submits a query (context) in each round, and the decision maker (DM) sequentially selects tokens irrevocably from a predefined token set. Once the sequence is completed, the DM receives a random utility from the user, whose expected value is determined by a sequence function that maps the chosen token sequence and the query to a non-negative real number.
Claims And Evidence: This paper make interesting claims which are suppoted by sufficient and strong evidences.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are well-reasoned. However, numerical results demonstrating their performance in real applications were not provided.
Theoretical Claims: The theoretical claims appear to be correct. Specifically, this work introduces a significant framework that effectively models the LLM decoding and alignment problem. While the problem itself is inherently challenging, it is addressed through an elegant assumption of DDMC, which provides a clever and practical solution.
Experimental Designs Or Analyses: Experiments are conducted to validate the empirical performance of the proposed methods.
Supplementary Material: I have reviewed the supplementary materials, which I believe significantly enhance the readability and clarity of the paper.
Relation To Broader Scientific Literature: The theoretical framework of tokenized bandits is novel, and the approach used to solve the problem is innovative.
Essential References Not Discussed: Essential references have been properly discussed.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None
Questions For Authors: None
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We truly appreciate your detailed feedback and insightful comments, in particular we are glad that the reviewer enjoys our problem and approach.
As the reviewer suggested, we agree that numerical results demonstrating our algorithm’s performance would greatly improve our paper - we appreciate your suggestion.
As such, we **evaluate our algorithm’s regret** with several benchmarks that we thought to be reasonable in our scenario.
We refer the reviewer to see: https://anonymous.4open.science/r/temp-03AC, directory /Regrets.
We evaluate algorithms based on **TLB model and LLM alignment scenario** presented in Section 5.1 with $\theta = [1/2,1/2,\ldots, 1/2]$, maximal length of sequence = 30, rounds 5000, and $\gamma = 0.8$.
We compare our EOFUL along with a benchmark and two other algorithms: (i) theoretical regret upper bound (under-scaled by 0.1 to make the plot more visible), (ii) WrongTheta that uses wrongly estimated $\theta = [-1/2,-1/2,\ldots,-1/2]$ and greedily decoding based on the weighted score, and (iii) Misaligned greedy that only greedily decodes with respect to the LLM’s probability.
Also, for practicality and computational efficiency, we only consider the top 15 tokens given by LLM in deciding the next token.
As observed in the figure, we observe that EOFUL effectively achieves sublinear regret.
Given that the regret upper bound is under-scaled,the actual performance may be much better than that of the theoretical guarantees.
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Rebuttal Comment 1.1:
Comment: Thank you for the responses to the reviewers. I really enjoyed reading this work and am inclined to accept it. That said, I believe there is still room for improvement, particularly by enriching the experimental section with more general cases (I noticed that similar concerns were also raised by other reviewers). Therefore, I will maintain my current score. | Summary: This paper introduces Tokenized Linear Bandit (TLB) and Tokenized Multi-Armed Bandit (TMAB), two variants of bandit algorithms designed for LLM decoding and alignment. These frameworks model LLM decoding as a sequential decision-making process, where a decision-maker selects tokens iteratively to form a complete sequence, receiving a random utility score based on user preferences. The authors establish that learning is impossible without structural assumptions and introduce a key assumption called Diminishing Distance with More Commons (DDMC), which enables efficient learning. They propose EOFUL (Excessive Optimism under the Face of Uncertainty) for TLB and GreedyETC (Greedy Exploration-Then-Commit) for TMAB, achieving sublinear regret bounds. A major theoretical insight is that greedy decoding can be optimal under DDMC, providing a justification for its effectiveness in LLM decoding. Empirical validation on Llama-3-8B with TruthfulQA and HH-RLHF datasets supports the DDMC assumption.
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### Update after rebuttal
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As mentioned further below, I am happy with the responses the authors provided. I think there is value in accepting this paper. Hoping there will be consensus among the reviewers that this is indeed the case.
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Claims And Evidence: The paper presents Tokenized Bandit frameworks (TLB and TMAB) for LLM decoding and alignment and supports its claims using rigorous theoretical analysis and empirical validation. Most of the claims are derived with clear mathematical proofs and sublinear regret bounds for EOFUL and GreedyETC. The empirical validation on Llama-3-8B with TruthfulQA and HH-RLHF provides some evidence that the DDMC assumption holds in practice. However, some strong baselines are not considered. For instance, ARGS (Alignment as Reward-Guided Search, Khanov et al., 2024), as a baseline, is missing. Comparing against ARGS, especially in terms of efficiency, performance, and scalability, could help clarify why a bandit framework is preferable to a search-based alignment method like ARGS.
Methods And Evaluation Criteria: The Tokenized Bandit framework (TLB & TMAB) is well-motivated for LLM decoding and alignment, as sequential token selection naturally fits a multi-armed bandit or linear bandit formulation. The authors provide a strong theoretical foundation and validate their approach on Llama-3-8B using TruthfulQA and HH-RLHF, which are reasonable benchmarks for alignment and factual correctness. However, the evaluation has some gaps: (1) No comparison to strong decoding-time alignment baselines like ARGS (Khanov et al., 2024), making it unclear if bandit-based alignment is superior to search-based alignment; (2) Limited diversity in test datasets, as evaluations focus only on two benchmarks, without testing broader alignment scenarios (e.g., safety-critical or adversarial tasks). While the evaluation is a good start, expanding it to stronger baselines and additional datasets would strengthen confidence in the method’s effectiveness.
Theoretical Claims: The paper provides rigorous mathematical proofs supporting its core claims, particularly: (1) Learning is impossible without structural assumptions in tokenized bandit settings, (2) Greedy decoding can be optimal under the Diminishing Distance with More Commons (DDMC) assumption, and (3) EOFUL (for TLB) and GreedyETC (for TMAB) achieve sublinear regret bounds. The derivations are logically consistent, following standard bandit theory techniques, and the regret bounds align with known results in linear and multi-armed bandits. However, the DDMC assumption lacks a formal justification for why it holds across different LLMs and datasets, relying primarily on empirical verification. To strengthen the theoretical foundation, the paper should provide (1) a more formal justification of DDMC beyond empirical trends.
Experimental Designs Or Analyses: The experimental design provides some validation of the Tokenized Bandit framework for factual correctness and preference alignment. However, the evaluation has significant gaps. While the regret bounds are well-structured, there is no explicit comparison to search-based alignment methods (e.g., ARGS) in terms of convergence speed or sample complexity. Additionally, the approach is not tested on more diverse datasets that could include safety-critical, adversarial, or instruction-following tasks to assess broader generalization. While the bandit framework is promising, these missing elements make it difficult to fully validate the empirical claims. Expanding the benchmarks and including stronger baselines would strengthen the study’s conclusions.
Supplementary Material: No, I didn't have the time.
Relation To Broader Scientific Literature: This paper builds on foundational work in multi-armed and linear bandits, adapting these frameworks to LLM decoding and alignment. It builds upon prior work on bandits to introduce Tokenized Bandit models (TLB and TMAB) that incorporate token-wise sequential decision-making. The Diminishing Distance with More Commons (DDMC) assumption is conceptually similar to structural constraints in regret minimization (Abbasi-Yadkori et al., 2011) but is newly applied to LLM decoding. Additionally, the paper is highly relevant to decoding-time alignment approaches such as ARGS (Khanov et al., 2024), which formulates alignment as a reward-guided search problem rather than reinforcement learning. However, the authors do not compare their work directly to search-based or reinforcement learning-based decoding strategies (e.g., PPO in RLHF), leaving a gap in understanding how bandit-based decoding fares against other methods.
Essential References Not Discussed: Khanov et al. "ARGS: Alignment as Reward-Guided Search" and follow-up works.
Other Strengths And Weaknesses: Please refer to the above sections.
Other Comments Or Suggestions: Overall, the paper is well-written. The problem is also well-defined and the proposed solution is clear.
Questions For Authors: Some of the questions that came to mind as I read the paper are detailed below. I am asking these questions in order to clarify/justify theoretical generalizability, empirical competitiveness, computational efficiency, and real-world robustness of Tokenized Bandits for LLM decoding and alignment.
1. How does the regret bound of EOFUL and GreedyETC compare to search-based decoding strategies like ARGS (Khanov et al., 2024) and variants?
2. Why is there no comparison to ARGS or reinforcement learning-based decoding strategies (e.g., PPO in RLHF)?
3. What is the computational efficiency of Tokenized Bandits compared to PPO-based RLHF and ARGS?
4. A well-known disadvantage for LinUCB is its computational complexity since it needs to incorporate historical information when initializing observation matrices and conducting matrix multiplication. Will the proposed approach inherits similar shortcomings?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We truly appreciate your insightful comments.
We will first make a general remark on our main contribution, and then answer each comment.
# General remark on main contribution
First, the main focus of our paper is to provide a **theoretical foundation** of tokenized versions of multi-armed bandits / linear contextual bandits, inspired by the tokenized decoding nature of the LLMs and applications such as LLM alignment / decoding.
As shown by our impossibility results (Prop 3.3 and Prop 4.1), we reveal that some assumptions are necessary for theoretical guarantees and we provide a fairly reasonable assumption along with a relaxed version of it (Appendix B) for that sake.
The need for certain assumptions in our setting (to learn a sequence function) are further justified by the fact that the seminal and related paper by Coquelin and Munos 2007 (see our Appendix C for more comparisons) impose a **rather stronger assumption** in the tree structure to obtain efficient algorithms.
They study bandit-based methods for tree search, motivated by real-world applications such as Go, and the objective is to learn a sequence function to maximize cumulative rewards.
They show that without any structural assumption on the tree, exponential dependency on the depth of the tree in regret is inevitable.
They pose a rather strong ‘smoothness’ assumption to obtain efficient algorithms.
Such assumption was deemed innocuous in their setting, though it was not even empirically validated and not intuitively justified.
Likewise, we impose an intuitive assumption tailored to our setting, validate it empirically, and provide a relaxed version.
We also conduct more experiments as per the reviewer’s request, which will be explained below.
# Comparison to ARGS / PPO in RLHF
Thanks for the pointer!
Regarding considering ARGS as a benchmark, the framework of ARGS cannot directly be applied in our setting, since ARGS assumes it have **access to an external reward function** and decode based on an weighted average between the original LLM’s probability and the reward.
Our framework, however, learns the latent reward function by observing user feedback via repeated interaction, without assuming such access.
Note that our regret is computed with respect to the offline benchmark that knows the latent parameter $\theta$ in hindsight, i.e. which can access the external reward function directly.
Thus, in some sense, ARGS can be thought of as the **offline algorithm** that knows the latent parameter in hindsight.
Regarding the reviewer’s comment in comparison to PPO in RLHF, we remark that our application on LLM alignment considers a **frozen LLM** that could not be retrained (e.g., for proprietary models not allowed to train or the user does not have the budget to train an LLM)" and tries to align the LLM in decoding time while learning the latent function that represents the portion of misalignment, so we think a direct comparison to PPO is irrelevant.
We also refer to **our response to Reviewer 9ZG7** for numerical evaluation of our algorithm.
# More justification on DDMC
Our DDMC assumption, or at least a relaxed version of it, is quite reasonable intuitively.
For instance, in extreme cases, if we append a lot of common tokens in each of two sequences of the same length, one could expect that the user will realize a similar experience of reading them.
Further, as we discussed in L#234, page 5, this shares similar intuition from the widely adopted submodularity on set functions.
Also, we conducted **more experiments** on more datasets and utility functions.
It can be found in https://anonymous.4open.science/r/temp-03AC.
In new experiments, we first tested DDMC assumption on two more datasets: AdvBench (standard jailbreak benchmark) and just-eval-instruct that contains many prompts of various tasks.
Further, we verified DDMC assumptions beyond our linear utility function, with L1/3/4 distance.
Overall, we observe a tendency that appending more common tokens decreases the utility gaps.
We will certainly add these in the revision.
# More questions
## 1. How does the regret bound of EOFUL..
As noted, frameworks like ARGS assume access to the reward function, so we cannot compare regrets.
## 2. Why is there no comparison…
We hope responses above clarified your question.
## 3. What is the computational efficiency...
Since PPO-based RLHF retrains the LLM itself, our approach has significantly less computational burden. Further, it is unfair to compare the computational complexity of our works to ARGS, as ARGS assumes access to the external reward function whereas our approaches need to learn it.
## 4. A well-known disadvantage of…
Good point! Similar to LinUCB, one can apply the standard lazy update to reduce the computational burden so that it needs to recompute the estimator only $O(log T)$ times. We refer to Section 5.1 in Abbasi-Yadkori et al., 2011 for more details. We will add a brief discussion on it in our revision.
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Rebuttal Comment 1.1:
Comment: I thank the authors for their rebuttal. Although I would have loved to see more detailed responses, I am happy overall with the rebuttal. I am maintaining my score. | null | null | null | null | null | null |
Enhancing Cooperative Multi-Agent Reinforcement Learning with State Modelling and Adversarial Exploration | Accept (poster) | Summary: The paper proposes a state modelling framework to infer meaningful beliefs about the unobserved state while filtering redundant information. It reconstructs other agents’ observations using an encoder-decoder. To overcome the sparse reward challenge, this paper proposes a adversarial count-based intrinsic exploration method to encourage the agents to visit novel states.
Claims And Evidence: The motivation of the proposed method is not clearly stated. It is hard to find the real contribution and innovation of the paper from the main contributions elaborated in the introduction.
This paper assumes that states contain information redundant for optimizing agents’
individual policies. Why make such an assumption?
What does the “adversarial targets” mean? Do you mean the target entity in the actual environment?
Methods And Evaluation Criteria: The paper uses an encoder-decoder to model the other agents’ observations based on only the local observation, which seems reasonable. To improve exploration, the paper encourages diversity of the latent variable z by using count-based intrinsic rewards.
This paper designs an adversarial exploration method to “discover novel, high-value states while improving the discriminative abilities of others”. But the count-based intrinsic reward only can drive agents to visit novel states. Such an intrinsic reward could not serve the purpose of encouraging the exploration of high-value states.
Theoretical Claims: I have checked the proof of the proposition 2.1.
Experimental Designs Or Analyses: This paper conducted evaluations on MPE, LBF, and RWARE. Experiments show that the proposed method outperforms the baselines in terms of learning speed and final performance. The algorithm has obvious advantages in sparse reward tasks.
Supplementary Material: I have reviewed the supplementary material, mainly the additional experiment results.
Relation To Broader Scientific Literature: This paper is linked to agent modeling and exploration in MARL.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
+ The experiments are good.
+ The proposed method is novel.
Main weaknesses:
+ The overall presentation of the paper lacks clarity. The writing of this paper needs further improvement. I believe that the quality of the paper will be greatly improved after improving the writing.
Other Comments Or Suggestions: + The citation format is incorrect.
+ In many figures, the legends obscure the main figures.
+ “Learning wi (and thus zi) w.r.t. policy optimization” Such a statement is difficult to understand.
+ Figure 1 could be presented in a better way. The current figure is difficult to read.
Questions For Authors: + What does the adversarial exploration and discriminative abilities mean? How you improve the discriminative abilities of other agents?
+ The method relies solely on local observations for agent modeling. Does it scale well as the number of agents increases?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate your time and input. We respond to your comments and questions below.
> 1. The motivation of the proposed method is not clearly stated.
We respectfully disagree with the reviewer's comment. In Lines 28-36 (right), we clearly state our main motivation for this paper: "we are interested in settings where agents lack explicit communication channels during execution. Such settings are of particular interest, because, while communication-based methods leverage inexpensive simulators for training, they may incur substantial computational overhead when executed in real-world environments". Moreover, in the intro (Lines 43 right– 64 left), we provide a detailed discussion of significant drawbacks and problematic assumptions of existing agent modelling (AM) methods. Remarkably, many of these claims (e.g., redundant state information, AM without exploration and policy optimization, single-agent AM) are empirically validated by our results and the extensive ablation study, demonstrating their detrimental impact on MARL performance. These challenges highlight the need for a more principled approach to AM in MARL and further motivate our approach.
> 2. Real contributions of the paper
Due to space constraints, please see our response to Question 7. in the rebuttal of reviewer CpzR.
> 3. This paper assumes that states contain information redundant for optimizing agents’ individual policies. Why?
This is an established assumption which has been validated by the NeurIPS paper ([48]-th reference in our paper) and the AAMAS paper [1], supported both by the curse of dimensionality and by intuitive reasoning. Specifically, in large and complex state spaces, each agent naturally prioritizes information that is more relevant or proximal to them while assigning lower importance to remote or less goal-related information.
> 4. What does the “adversarial targets” mean? Do you mean the target entity in the actual environment?
The term "targets" has been used many times before the adversarial exploration section (e.g., see lines 155 right, 214 left, 175 right, 181 right, 185 right, 187 right, 195 right) in the paper to denote the reconstruction targets of the encoder-decoder.
> 5. This paper designs an adversarial exploration method to “discover novel, high-value states while improving the discriminative abilities of others”. But the count-based intrinsic reward only can drive agents to visit novel states. Such an intrinsic reward could not serve the purpose of encouraging the exploration of high-value states.
Thanks for this comment. By the means of adversarial exploration, each agent is motivated to reach novel states, while she challenges the state modelling abilities of other agents. By doing so, our exploration schema aims at improving the joint belief about the joint state, and thus the joint policy, as the policy network of each agent uses her belief as extra input. Therefore, our method is more likely to reach novel, high-value states than the original which hashes observations.
> 6. The citation format is incorrect. In many figures, the legends obscure the main figures. Figure 1 could be presented in a better way.
Thanks for your comments. We will fix these minor typos in the camera-ready version. Regarding Fig. 1, we have thoroughly explain its components in high-level in Lines 147 (right) - 169 (left).
> 7. What do the adversarial exploration and discriminative abilities mean?
Thanks for this question. By discriminative abilities of an agent under partial observability we mean the ability of the agent to identify meaningful information about the unobserved global state based on her local information. In other words, discriminative abilities represent how well the agent models the global state. Our approach defines the meaningful state information within the state modelling framework (see lines 129 left - 158 left).
Adversarial exploration is extensively explained and motivated in Lines 246 (left) - 267 (left).
> 8. The overall presentation of the paper lacks clarity
We kindly disagree with the above comment that there are major presentation issues about the paper. Reviewer hakk finds that "*the paper was clear and easy to follow, which made understanding the ideas very smooth and engaging*". Some of the points you found unclear are thoroughly explained earlier in the paper, so we believe there is a chance that you missed these explanations and this rendered the points, our motivation and contributions unclear. If this is the case, we hope through a more careful reading to appreciate our ideas and results more. Otherwise, if you insist that there are specific points which require better explanation from our end, please let us know to fix them.
> 9. Scalability with more agents
Thanks for this question. See our response to reviewer hakk on question 1.
[1] Li et al. From explicit communication to tacit cooperation: A novel paradigm for cooperative MARL. 2024 | Summary: The paper presents a novel approach to cooperative multi-agent reinforcement learning (MARL) under partial observability by introducing a state modelling framework combined with adversarial exploration. In this framework, each agent infers a latent belief from its local observation using a variational encoder–decoder, while learnable agent modeling filters remove redundant features to capture essential global state information. The resulting SMPE2 algorithm leverages these latent beliefs by incorporating them into the policy network and using count-based intrinsic rewards to encourage exploration of novel, high-value states, thereby enhancing coordination and overcoming sparse-reward challenges. Experimental results on benchmarks like MPE, LBF, and RWARE show that SMPE2 outperforms state-of-the-art methods, leading to faster convergence and higher episodic rewards.
## Update After Rebuttal
Thanks for the authors' rebuttal. However, I still feel like this paper is short of reasonable justifications. The explanations provided by the authors stand on their own suppose with no sufficient evidence to back up. Although the authors emphasized their work is theoretically sound, I have different understanding on this point. As a result, I think of this paper is not ready for publication at this moment. I suggest the authors may link their modeling and approach to some realistic implication, which is always the aim of engineering.
Claims And Evidence: ### Supported Claims
1. The authors have empirically demonstrated the effectiveness of each component of the proposed algorithm SMPE2.
2. The authors claimed that "The framework assumes that the joint state information can be redundant and needs to be appropriately filtered in order to be informative to agents." This has been partially verified by visualizing weight functions.
3. The authors claimed that "Intuitively, $w_{i}$ has an AM interpretation, as it represents the importance of each of other agents’ information to agent i’s state modelling." This has been verified by one example.
4. The authors claimed that "Note the importance of the AM filter $w_{i}$: (a) With it, although the target of ED grows linearly
with the number of agents, only features that can be inferred through $z_{i}$ remain as part of other agents’ observations in the reconstruction loss. (b) Without it, it would be challenging to infer meaningful embeddings $z_{i}$, due to non-informative joint state information." These two conditions have been verified by showing ablation study and visualizing the the projected $z_{i}$ by t-SNE.
### Problematic Claims
1. In introduction (Line 59-64), the authors blame that previous work drew multiple assumptions. This is not convincing to be a motivation. The main reason is that those assumptions are primarily used to estimate the boundary of methods. In other words, no assumptions does not imply the effectiveness to all scenarios, except that you can prove that rigorously in mathematics or do experimentation in all possible scenarios. Especially, I find that this paper also made several assumptions, such as the one illustrates the relation between latent space and observation (Line 181-184).
2. The authors claimed that the belief $z_{i}$ contains meaningful information about the unobserved state, informative for optimizing the agent's own policy. This assumption is quite strong, for example, how is this guaranteed?
3. As for the definition of conditions for non-informative joint state feature, the authors claimed that "it cannot be inferred through $z_{i}$, in the sense that the agent cannot predict it conditioned on its own observation due to partial observability and non-stationarity." This condition is extremely strong, as it rules out information that may be beneficial to agent decision making, but not acquired due to the belief space the authors defined. As I haven't seen any clear and concrete definition for the belief space, this condition is vague. I suggest the authors can have more rigorous discussion here.
4. The authors claimed that "using the full state information as an extra input to the policy, even when utilizing a compressed embedding, may harm performance due to redundant state information non-informative to agent $i$." This may be due to the information loss brought by compression to get $z_{i}$, rather than the redundant state information.
5. The authors claimed that "Following the definition of the state modelling problem, we aim to ensure that $w_{i}$ (and thus $z_{i}$) incorporate information relevant to maximizing $V^{\pi}$ and thus, $w_{i}$ to be capable of filtering non-informative state features irrelevant to maximizing agent’s future rewards." Although the weight $w_{i}$ is learnable, I am afraid it could be not effective to filter out the non-informative information. For example, even though the weight converges to including partial non-informative, I believe it can still find a local optimum by policy. More importantly, this suboptimality is difficult to be verified.
Methods And Evaluation Criteria: ### Methods
From the high-level view, the proposed method makes sense to the research problem this paper aims to solve. However, as the proposed method is constituted of multiple components, it is difficult to make a coherent understanding of the proposed method from the theoretical perspective.
### Evaluation Criteria
This paper is different from other regular papers in MARL. It has conducted a lot of abalation studies from diverse dimensions, such as visualizing the learned features. This is the most critical benefit of this paper.
Theoretical Claims: This paper has a simple theoretical claim. I have checked the proof and it should be correct.
Experimental Designs Or Analyses: This paper has designed plenty of experiments, motivated by several research questions. I have checked these in detail, and I believe all these are sound. In addition, the experimental analyses also seem reasonable.
Supplementary Material: I have come across all the contents in Supplementary Material.
Relation To Broader Scientific Literature: This paper mainly investigates a long-standing problem in collaborative MARL, exploration and improving coordination in decentralized policies (or independent learning). The general framework proposed in this paper has no big difference from the previous work, for example, learning embeddings representing other agent behaviors [1,2] and using intrinsic reward to improve exploration [3].
[1] Papoudakis, Georgios, Filippos Christianos, and Stefano Albrecht. "Agent modelling under partial observability for deep reinforcement learning." Advances in Neural Information Processing Systems 34 (2021): 19210-19222.
[2] Mahajan, Anuj, et al. "Maven: Multi-agent variational exploration." Advances in neural information processing systems 32 (2019).
[3] Pathak, Deepak, et al. "Curiosity-driven exploration by self-supervised prediction." International conference on machine learning. PMLR, 2017.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: ### Other Weaknesses
This paper is not easy to comprehend. The main reason is that it has included too much information, with an overall description that establish a logic chain through all these components of the proposed method. Moreover, it is not easy to track the main contribution of this paper. It seems like a compound of several technical tricks.
Other Comments Or Suggestions: I suggest the authors can re-organize the writing in a more logical way, to emphasize the most critical contribution delivered by this paper.
Questions For Authors: 1. The authors are requested to address the concerns in **Claims And Evidence**.
2. In addition, I believe MAVEN [1] is highly related to the framework proposed in this paper, except that it does not include an additional intrinsic reward term. For this reason, I would like to see the additional experiments for comparison between the proposed method and MAVEN.
3. The authors claimed that "Agent is intrinsically motivated to discover novel $o_{i}$ (which lead to novel $z_{i}$) which at the same time constitute unseen targets for the others’ reconstruction training. Therefore, these targets aim to adversarially increase the losses of other agents’ reconstruction models." Do the authors mean the mismatch between each agent's information due to independent update?
4. The authors claimed that "To do so, given that $z_{i}$ is solely conditioned on $o_{i}$, the agent is implicitly motivated to discover novel observations that must lead to novel $z_{i}$." What is the logic here? Can the authors provide more evidence to clarify this claim?
[1] Mahajan, Anuj, et al. "Maven: Multi-agent variational exploration." Advances in neural information processing systems 32 (2019).
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: > 1. Motivation and Discussion about Assumptions of related work
We respectfully disagree with the reviewer's comment. In the introduction (Lines 43–64), we provide a detailed discussion of significant drawbacks and problematic assumptions of existing agent modelling (AM) methods. Remarkably, many of these claims (e.g., redundant state information, AM without exploration and policy optimization, single-agent AM) are empirically validated by our results and the extensive ablation study, demonstrating their detrimental impact on MARL performance. These challenges highlight the need for a more principled approach to AM in MARL. Regarding Lines 59–64, we believe that the assumptions outlined — namely, a priori knowledge of state features, centralized execution, and a focus solely on team games — are quite restrictive. These constraints limit the practicality of such algorithms, making them less applicable to a wide range of real-world scenarios.
> 2. Assumption: z_i contains meaningful information about the unobserved state, informative for optimizing the policy.
Assuming that there exists a latent belief space which contains unobserved state information meaningful for optimizing the policy has been very standard in AM (e.g., see [40, 42, 44]). We note that this is the main assumption in order for AM to be applicable under partial observability.
> 3. It rules out information that may be beneficial to decision making, but not acquired due to the defined beliefs.
The reviewer must have misunderstood that according to our definition if a state feature is beneficial to decision making, then the framework considers this feature to be "informative" (see first bullet, line 139). Such a feature could be identified by w_i, and thus z_i, being conditioned on w_i, is informative of this feature during exploration. Also, our definition implies that if a feature cannot be inferred through z_i and it is not relevant to policy optimization, then this feature is "not-informative".
> 4. Comment on "even when utilizing a compressed embedding"
Thanks for this comment. It is known from [9] that providing full state information as an additional input to the policy can degrade performance due to redundant, non-informative state features. In our work, we demonstrate that this issue can persist even when using a compressed embedding z_i, as shown in Fig. 5 (left), where applying filters leads to improved performance. We will ensure that this detail is clarified in the final version.
> 5. Even though the weight converges to including partial non-informative, it can still find a local optimum by policy. More importantly, this suboptimality is difficult to be verified.
Due to space constraints, please see our response to Question 8. in the rebuttal of reviewer CpzR.
> 6. Difference from LIAM, MAVEN and [3]
Due to space constraints, please see our response to Question 10. in the rebuttal of reviewer W3Cu.
> 7. Multiple components: difficult to understand from the theoretical perspective
We believe that all loss components have been well-explained in Sec. 3 and are well-validated by a plethora of experiments (see Fig. 5, 7, 15 - 26). More specifically, from a theoretical standpoint we give detailed intuition of each component:
1. L_rec: 172 left - 182 right
2. L_wcritic: 213 left - 218 left
3. intrinsic reward: Sec. 3.2
4. L_norm: 196 left - 200 left
5. L_KL: 202 left - 207 left
Our method does not rely on "tricks" but on **conceptual components** (1–3), motivated by how we think of the ideal MARL behavior against partial observability (see Lines 77-92 (left) and 98-104 (right)). The components 4–5 were introduced to ensure that the proposed method is theoretically sound (also illustrated in Fig. 7, 17) and adheres to our definition of state modeling (lines 152 & 205 left).
> 8. Not easy to track the main contribution of this paper
Due to space constraints, please see our response to Question 7. in the rebuttal of reviewer CpzR.
> 9. Comparison to MAVEN
Due to space constraints, please see our response to Question 6. in the rebuttal of reviewer CpzR.
> 10. Question about "intrinsically motivated...models"
Since each agent updates its policy independently, conditioned only on its own observations and beliefs, it is intrinsically motivated to seek novel observations o_i, thereby discovering novel z_i. However, since o_i serve as part of the target for other agents' decoders, they inadvertently increase the reconstruction loss of those agents.
> 11. Question about "To do so...z_i."
Since z_i is a function of only o_i, and agent i is motivated to reach novel z_i, then the only way for the agent to achieve this is by discovering novel o_i that lead to novel z_i. In Appendix E.4.7 we show how we effectively handle the dynamic nature of the reward.
[@] Papadopoulos et al. (AAMAS 2025) - An Extended Benchmarking of Multi-Agent Reinforcement Learning Algorithms in Complex Fully Cooperative Tasks. | Summary: In most Multi-Agent Reinforcement Learning (MARL) problems, agents operate under partial observability, making decisions based on their observations and beliefs rather than the full state, and a naïve integration of the full state to each agent’s observation can introduce irrelevant information, hinder exploration, and degrade performance. To address this, the paper proposes a state modelling framework that enables agents to construct meaningful beliefs about the unobserved state, optimizing their policies and improving exploration. The authors introduce State Modelling for Policy Enhancement through Exploration (SMPE2), which consists of two components: (1) self-supervised state modelling, where an encoder-decoder predicts other agents' observations using only local information while Agent Modelling filters that remove redundant joint-state features, and (2) adversarial count-based intrinsic exploration, an intrinsic reward mechanism that uses SimHash-based novelty detection to guide exploration toward novel, high-value states. Empirical results on MPE, LBF, and RWARE show SMPE2 outperforms state-of-the-art MARL baselines, with extensive ablation studies confirming the importance of its components.
Claims And Evidence: The paper claims that the state modelling objective is equivalent to the Dec-POMDP objective, providing a proof in Appendix D.
Their claim that state modelling improves MARL performance is supported by empirical evidence from a variety of scenarios: dense (MPE), balanced sparse (LBF), and very sparse (RWARE) reward settings. Additionally, they demonstrate that SMPE2 is flexible, as it can be applied to different MARL algorithms, where they experiment in the main paper using MAA2C as the backbone. Additional results in the appendix show SMPE2-MAPPO outperforming MAPPO as well.
The authors further claim that AM filters retain only informative state features, preventing redundant information from degrading performance, while adversarial exploration guides agents toward high-value states, improving cooperation and exploration. Ablation studies confirm that removing these components hinders learning and slows convergence.
A major concern regarding the validity of these claims is the performance of SOTA algorithms on the suggested scenarios. To my knowledge, the only literature that uses RWARE hard scenarios is [1] which compare their work using different baselines, besides a recent paper [2] that shared the same scenarios choice, however, another study using a JAXified version of these environments [3] suggests that MAPPO performs well in the proposed RWARE settings.
**Reference:**
[1] Christianos et al. (2021) - Shared Experience Actor-Critic for Multi-Agent Reinforcement Learning.
[2] Papadopoulos et al. (2025) - An Extended Benchmarking of Multi-Agent Reinforcement Learning Algorithms in Complex Fully Cooperative Tasks.
[3] Mahjoub et al. (2025) - Sable: A Performant, Efficient, and Scalable Sequence Model for MARL.
Methods And Evaluation Criteria: The paper evaluates SMPE2 in three environments (MPE, LBF, and RWARE) and compares it against MAA2C, COMA, MAPPO, ATM, EMC, MASER, and EOI. The selection of some baselines is well motivated, as some incorporate state modelling per agent, such as EOI, and MASER. The authors provide detailed information on computational resources, hyperparameters, and benchmark settings, ensuring reproducibility.
However, I have a few concerns regarding the evaluation:
1. Scenarios selection: The authors use customized LBF and hard RWARE scenarios to showcase exploration skills. While this approach is valid, it would be beneficial to reinforce these findings on well-established scenarios from the literature [4]. This would allow for more direct comparisons with prior works.
2. Scalability and harder settings: Further evaluation on larger-scale environments, such as RWARE larger grid and more agents (e.g., customized environments like large-8ag), could better assess SMPE2's performance in harder exploration settings with more agents. Given that many SOTA MARL algorithms may struggle to provide any signal in such settings, testing on these variants would further reinforce confidence in SMPE2's state modelling and exploration strategies.
3. Hyperparameter tuning details: The paper does not specify how hyperparameters were tuned, how many trials were conducted, or whether tuning was performed per scenario or per environment.
4. Suggestion to increase the number of seeds: The experiments are conducted on six random seeds, but increasing to ten seeds would improve statistical robustness, as discussed in [5,6].
**References:**
[4] Papoudakis et al. (2021) - Benchmarking Multi-Agent Deep Reinforcement Learning Algorithms in Cooperative Tasks.
[5] Agarwal et al. (2021) - Deep RL at the Edge of the Statistical Precipice.
[6] Gorsane et al. (2022) - Standardized Performance Evaluation in Cooperative MARL.
Theoretical Claims: The paper presents Proposition 2.1, claiming that the state modelling objective is equivalent to the Dec-POMDP objective.
Experimental Designs Or Analyses: The experiments are well-structured, with effective ablation studies highlighting each SMPE2 component’s impact. However, the authos evaluate their method using customized scenarios and ones not commonly used in prior work, including additional well-established tasks from the same settings (MPE, LBF and Rware) and additional environments in general would provide more reliable comparisons and further validate SMPE2. Additionally, I would suggest to briefly explaining t-SNE before using it in Figure 7, as some readers may not be familiar with its purpose in the ablation study.
Supplementary Material: The appendix is rich in content, providing additional experimental results for MPE, related work, technical details of SMPE2's implementation, training stability analysis, pseudocode, and more. However, as mentioned in Methods and Evaluation Criteria (3rd point), it would be valuable to include details on hyperparameter tuning, such as the number of trials, tuning methodology, and whether tuning was done per scenario or per environment.
Relation To Broader Scientific Literature: The paper builds on opponent modelling approaches like LIAM, SIDE, and MAVEN, but focuses on improving state representation learning rather than directly modelling other agents. The SimHash-based intrinsic reward mechanism aligns with previous count-based exploration techniques but introduces an adversarial component, distinguishing it from prior methods. In CTDE-based MARL, SMPE2 follows the centralized training decentralized execution (CTDE) paradigm, similar to MAPPO and COMA, but incorporates self-supervised learning for belief state inference, making it a novel contribution to the field.
Essential References Not Discussed: Despite using the transformer-based algorithm ATM, the paper lacks discussion on other SOTA transformer-based MARL methods, such as [7], which explore sequence-based representation learning as an alternative to state modelling. Additionally, it does not reference heterogeneous-agent reinforcement learning, such as [8], which studies how agents with different capabilities and roles coordinate in MARL settings. And lastly, the paper did not mention Shared Experience Actor-Critic (SEAC) [1], which focuses on improving exploration by sharing experiences among agents.
**References:**
[7] Wen et al. (2022) - Multi-Agent Reinforcement Learning as a Sequence Modeling Problem.
[8] Zhong et al. (2023) - Heterogeneous-Agent Reinforcement Learning
Other Strengths And Weaknesses: **Strengths:** The work is novel and provides thorough ablation studies that effectively address most questions regarding component choices.
**Weaknesses:** The computational overhead is a concern, especially when scaling to larger agent populations with such a complex network. The authors report that SMPE2 is approximately 25× faster than MASER, 30× faster than EMC, 17× faster than EOI, and 2× faster than ATM, but this comparison was done on LBF:2s-12x12-2p-2f, which only includes two agents. It remains unclear whether this speed advantage holds as the number of agents increases.
Other Comments Or Suggestions: The paper was clear and easy to follow, which made understanding the ideas very smooth and engaging.
**Syntax Suggestions:**
1. Line 44: A comma should be added for better readability.
2. "Due to space constraints, ...": This phrase appears multiple times, but it would be better to directly reference the appendix section without justifying why it's not in the main text.
3. Line 173 ("we aim agents") : This phrasing feels incorrect; rewording would improve clarity.
**Plot Suggestions:**
1. Legends placement: Currently, all legends are placed on top of the x-axis. It would be better to move them above the plots or slightly below for visibility.
2. Figure 5 (left plot): The legend is cropped at the edge, slightly reducing the plot's clarity.
3. Figure 14: The legend redundantly repeats algorithm names twice.
**Clarity Suggestion:**
- The paper uses the format “(number)” for both citations and equations, which can be confusing for readers when referencing them in text. It would help to distinguish them visually, perhaps by adding brackets or a different formatting style for references.
Questions For Authors: First of all, I would like to acknowledge the thorough ablation studies in the paper. Each time I had a question about a component choice, I later found that an ablation study had already addressed it, which was great to see.
That said, I still have a few questions:
1. While the results demonstrate SMPE2’s strong performance on the tasks considered, it would be helpful to explain in more detail why certain SOTA algorithms struggle in specific scenarios. Additionally, could you provide more details on the hyperparameter tuning process: how were the parameters selected? Lastly, I strongly encourage testing on well-established scenarios from the literature (e.g., from [4]), as this would allow for direct comparisons with prior works and further reinforce SMPE2’s improvements.
2. The reported speedup comparisons are based on LBF with two agents. Does this efficiency hold for larger-scale environments, or would state modelling and AM filters introduce bottlenecks?
3. Given that ATM (a transformer-based algorithm) was included, why was Multi-Agent Transformer (MAT) [7] not considered? Would SMPE2’s state modelling be complementary or redundant in transformer-based architectures?
4. SMPE2 uses parameter sharing in LBF and RWARE but not in MPE. Did you test fully independent policies across all environments, and how does removing parameter sharing affect performance? Additionally, do the baseline algorithms use parameter sharing?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate your time and input. Please see our responses below:
> 1. Scalability with more agents
Thanks for this question. Along with Spread-8 and LBF 7s-20x20-5p-3f (see Fig. 2, 3), we also add results on other large LBF tasks: namely 8s-25x25-8p-5f and 7s-30x30-7p-4f. We note that these tasks have been benchmarked by the AAMAS2025 paper [1]. Below, we show that SMPE outperforms all baselines in these tasks as well.
|Env |SMPE | MAA2C |MAPPO|MASER| EOI | ATM
|-----------------:|---------:|--------:|----------:|----------:|------:|-----:|
| 8s-25x25-8p-5f| **0.64 +- 0.12**|0.52 +- 0.24|0.41 +- 0.23|0.01 +- 0| 0.07 +- 0.02 | 0.36 +- 0.28 |
| 7s-30x30-7p-4f| **0.74 +- 0.02**|0.71 +- 0.02 |0.57 +- 0.03|0.01 +- 0| 0.04 +- 0.01 | 0.59 +- 0.04 |
> 2. Computational overhead: SM and AM filters a bottleneck?
Thanks for this question. From the table below, we observe that even in larger settings, SM and AM filters only introduce a moderate (and completely justified) extra computational overhead, less than ATM, and far less than EOI, EMC and MASER.
|Env|SMPE |MAA2C|MAPPO|MASER |EOI|ATM|EMC|
|-----------------:|---------:|--------:|----------:|----------:|------:|-----:|-----:|
| 25x25-8p-5f| 0d 7h |0d 2h | 0d 3h | 1d 5h| 1d 20h | 0d 8h| 4d 12h|
| Spread-8| 0d 9h |0d 4h|0d 5h |2d 5h |3d 9h | 0d 18h | 5d 3h|
> 3. Evaluated scenarios
Thanks for this comment. All LBF and RWARE tasks from [41] are not difficult to solve. More specifically, the RWARE tasks from [41] are not the -hard ones. Moreover, in all LBF tasks from [41] (most of them are cooperative-competitive, that is an easier version of the problem), our method converges fast to an optimal policy. This is the main reason we selected more challenging scenarios from these benchmarks.
Remarkably, [1] benchmarks all of our selected tasks and explicitly highlights as open challenges most of our LBF tasks along with MPE tasks with 5 or more agents, in all of which SMPE performs significantly better than all baselines.
> 4. Why was MAT not considered? SM in transformer-based architectures?
Thanks for this question. Since both ATM and MAT are transformer-based algorithms, we chose to include only one of them to ensure a more diverse set of baselines, rather than over-representing algorithms from the same direction of approaches. We selected ATM over MAT because MAT is not implemented in (E)PyMARL, whereas ATM and all other baselines we consider are. This ensures that all methods are evaluated under the same protocol. Additionally, MAT has already been benchmarked in the same environments (see [1]), where it generally underperforms compared to our baselines. Notably, the authors have not highlighted MAT as a "best" algorithm. Regarding if SMPE would fit a transformer-based architecture, we have not evaluated it yet and we have left this direction as a future work.
> 5. hyperparameter tuning, such as the number of trials, tuning methodology, whether tuning was done per scenario or per environment, and parameter sharing.
Thanks for this comment. We followed [41]: For hyperparameters, optimization was performed for each algorithm separately in each environment (not scenario). Then from each environment, we selected one task and optimised the hyperparameters of all algorithms in this task. We evaluated algorithms using 6 independent runs (seeds).
Except for MPE, where [41] (and also [1]) noted that parameter sharing was more detrimental, we used parameter sharing for all other tasks across all algorithms. All evaluated algorithms ran with the same configuration in parameter sharing. We selected the configuration of parameter sharing based on [1,41], and we did not run further experiments with independent/sharing policies.
> 6. Validity of MAPPO results
Thanks for this comment. We evaluated MAPPO using the EPyMARL code and adhered to the same parameters as in [41]. We are confident that all baselines were run correctly, and we can upload all log files to a GitHub repository after the camera-ready version. As the reviewer pointed out, our MAPPO results are on par with those reported in the AAMAS 2025 paper [1], where we verified that the algorithm and environment hyperparameters were the same. In contrast, [2] does not use the (E)PyMARL library, which could lead to significant differences in the evaluation protocol. Moreover, we find it peculiar that MAPPO manages to reach good performance far before 20M steps (e.g. in 2ag-tiny-hard, 4ag-small-hard). We also conducted additional experiments with different random seeds, but we did not observe the behavior described.
> 7. References Not Discussed and further suggestions
Thanks for this comment. We will make sure to incorporate all suggestions.
[1] Papadopoulos et al. (2025) - An Extended Benchmarking of Multi-Agent Reinforcement Learning Algorithms in Complex Fully Cooperative Tasks.
[2] Mahjoub et al. (2025) - Sable: A Performant, Efficient, and Scalable Sequence Model for MARL. | Summary: This paper proposes State Modelling for Policy Enhancement through Exploration, a novel approach to cooperative multi-agent reinforcement learning in partially observable environments without communication. The method enables agents to infer meaningful belief representations about unobservable states through variational inference and self-supervised learning, while filtering out redundant information. The authors claim to enhance agents' policies both explicitly by incorporating these beliefs into policy networks and implicitly through adversarial exploration. Experiments across three benchmarks demonstrate that the proposed consistently outperforms state-of-the-art MARL algorithms, particularly in cooperative tasks that require extensive coordination and exploration.
Claims And Evidence: The authors provide theoretical justification (Proposition 2.1) showing that their state modelling objective equals the DecPOMDP objective. They perform extensive experiments on three benchmark environments (MPE, LBF, and RWARE) against multiple baselines with results that agree with their claims.
Methods And Evaluation Criteria: The evaluation metric (unnormalized average episodic reward) is common. The authors report results with confidence intervals averaged over six random seeds, which is sufficient for statistical significance. I appreciate not doing mean and standard error. The authors also properly analyze their method through ablation studies to verify the contribution of each component.
Theoretical Claims: The authors refer the proof to Proposition 2.1 as “missing proof”. I am not sure what that entails. The proof is sound and follows from the fact that the set of policies encompassed by the state modelling framework includes all policies that could solve the original problem. However, I am not familiar with this methodology.
Experimental Designs Or Analyses: The experimental designs and analyses appear sound. The authors use established benchmarks with appropriate configurations and metrics. The ablation studies are well-designed to isolate the contributions of different components.
One concern I have is that some figures show inconclusive results. A more detailed analysis in the style of rliable [1] could be more informative than some subfigures in Fig 3 and 4.
One minor concern is that the evaluation in MPE Spread with increasing number of agents (3, 4, 5, 8) doesn't fully demonstrate the scalability of the approach with even larger numbers of agents.
[1] Agarwar et al, Deep Reinforcement Learning at the Edge of the Statistical Precipice
Supplementary Material: I reviewed the supplementary material, which includes:
Extended related work
Additional experimental results on MPE
Extended preliminaries on MAA2C and MLIAM
The proof of Proposition 2.1
Extended experimental setup with benchmark details
Extended ablations
Algorithm pseudocode
The supplementary material provides comprehensive information to understand and potentially reproduce the experiments.
Relation To Broader Scientific Literature: The state modelling framework extends previous agent modelling approaches by learning representations with respect to policy optimization rather than as an auxiliary task. This addresses a limitation in previous works such as "Agent modelling under partial observability for deep reinforcement learning" (Papoudakis et al., 2021) where the aim is to learn a relationship between the trajectory of the controlled agent and the modelled agent. The paper also suggests the use of adversarial methods.
The use of AM filters to handle redundant state information is motivated by findings in "Efficient multi-agent communication via self-supervised information aggregation" (Guan et al., 2022) where the authors aggregate the information through an attention mechanism. Note that the authors mention the same work twice for no reason as two separate entries.
The adversarial exploration schema uses hashing as done in "# exploration: A study of count-based exploration for deep reinforcement learning" (Tang et al., 2017), but applies it in a novel way to the multi-agent setting. I really like the paper’s study of the smoothness of the intrinsic reward smoothness rate.
Essential References Not Discussed: The paper appears to cover the most relevant related works in MARL, agent modelling, and exploration. However, it could benefit from discussing:
1) More recent work on belief representation learning in MARL, such as approaches using transformers or other sequence modeling techniques to handle partial observability.
2) More extensive comparison with world models or model-based MARL approaches
Other Strengths And Weaknesses: The paper is well-written with consistent notations and the clearly stated questions throughout the main body make the paper easy to follow. The formulas are clear and the notation is consistent. Figure 1 is not entirely clear and the arrow convention is not sufficient to distinguish the gradient and the data flow. This work could benefit a lot from more justification on how the baselines are selected, especially the ones that are fairly simpler than the proposed method.
The paper has a clear ablation study but I would like to see more details on how a method with this many components can scale up to more complex settings.
Other Comments Or Suggestions: Check Figure 1 and more scalability analysis. Figure 3 and 4 have inconclusive results in some subfigures, it is very clear which ones.
Line 262 first column has a typo: “By doing do”
The Guan et al. paper is mentioned twice in the reference section. Both as 9 and 10. Please fix
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your time and input, along with the positive evaluation. We respond to your comments and questions below.
> 1. A more detailed analysis in the style of rliable [42] could be more informative than some subfigures in Fig 3 and 4.
Thanks for this comment. We will consider using rliable in the camere-ready version.
> 2. Scalability with more agents
See our response in question 2. to reviewer W3Cu
> 3. Comment on missing related works
Thank you for this comment. Does the reviewer some specific reference in mind? We will be happy to add missing related works.
> 4. Figure 1 is not entirely clear and the arrow convention is not sufficient to distinguish the gradient and the data flow.
Thank you for this comment. Our overview of SMPE^2 and the arrow convention follows a visualization approach similar to that of many well-established MARL papers (see [43], [44], [46]). If the reviewer still has objections about the figure, we are open to discuss possible improvements.
> 5. Note that the authors mention the same work twice for no reason as two separate entries. Line 262 first column has a typo: “By doing do”. The Guan et al. paper is mentioned twice in the references. Line 1194 should be well-entagled instead
Thanks! We will fix these minor typos.
**Due to space constraints, below we include responses to some of the questions of the other reviewers.**
> 6. Comparison to MAVEN
We add experimental comparison with MAVEN on challenging RWARE and LBF scenarios. We use the mean values over 6 seeds. Our method significantly outperforms this method.
|Method |rware-small-4ag-hard |rware-tiny-4ag-hard|lbf:4s-11x11-3p-2f|
|-----------------:|---------:|--------:|----------:|
| SMPE| **6.3**|**20.1**|**98.3**|
| MAVEN| 1.3|7.8|0.9|
> 7. Real contributions of the paper
Regarding the main contributions, they have been extensively highlighted:
- in the introduction (Lines 94 left - 69 right)
- in a series of research questions (Q1-Q8) we address
- in important results (e.g., see lines 320-326 right: these tasks have been viewed as open challenges by [@])
- in section 3
Based on the above, the main technical contributions of our paper are the following: We propose the state modelling optimization framework, on top of which we propose the SMPE MARL method. Based on state modelling, each agent of SMPE aims at learning meaningful beliefs about the unobserved global state, from each own perspective, by trying to predict what the other agents observe, and use her belief in order to enhance her own individual policy. To ensure that the beliefs of each agent are informative to her decision making, the framework entails learning of the belief with respect to her policy optimization. Moreover, SMPE introduces the AM filters which aim to filter out redundant global state information which may be detrimental to the inference of the beliefs, and thus of the MARL performance. Our approach introduces two novel loss objectives for learning the beliefs and the AM filters of each agent: (a) a reconstruction loss for learning the AM filters via a self-supervised manner, which ensures that the AM filters identify global state features that can be inferred by the formed agents' belief of the agent, and (b) an RL loss that ensures that the inferred beliefs incorporate information relevant to her policy optimization through backpropagation on the AM filters. Additionally, our method further harnesses the rich state information captured by the agents' beliefs. Each agent uses a count-based intrinsic reward on her own agent belief. This simple exploration schema is proved to be of great importance for joint exploration under partial observability, by encouraging each agent to discover novel observations and also by helping other agents form better explored beliefs about the unobserved global state through the means of an interesting adversarial competition. Remarkably, our experiments validate each of the above conceptual component of our method, and also suggest that SMPE outperforms state-of-the-art methods in challenging, well-established benchmarks.
> 8. Even though the weight converges to including partial non-informative, it can still find a local optimum by policy. More importantly, this suboptimality is difficult to be verified.
Our method controls the contribution of L_rec and L_wcritic to the AM filters through the selection of the hyperparameters: $lr_{wcritic}$ (learning rate in L_wcritic) and $lr_{w}$ (learning rate in L_rec). In practice, we found that a good hyperparameter selection is to set $lr_{wcritic}$ 100 times smaller than $lr_{w}$ (see Table 3, appendix), so that policy optimization does not impede reconstruction. One way to verify if the weight is trained well w.r.t. policy is by looking at the cumulative reward. This is because w affects z and thus both the policy and exploration. In our results (e.g., see Fig. 5) we consider that w is near-optimal w.r.t. policy. | Summary: This paper proposes State Modelling for Policy Enhancement through Exploration, a novel approach to cooperative multi-agent reinforcement learning in partially observable environments without communication. The method enables agents to infer meaningful belief representations about unobservable states through variational inference and self-supervised learning, while filtering out redundant information. The authors claim to enhance agents' policies both explicitly by incorporating these beliefs into policy networks and implicitly through adversarial exploration. Experiments across three benchmarks demonstrate that the proposed consistently outperforms state-of-the-art MARL algorithms, particularly in cooperative tasks that require extensive coordination and exploration.
## update after rebuttal
I have interacted with the authors and my concerns were addressed. I think it is really important to add more details addressing the strength of contribution concerns by the other reviewers for the camera ready version in case of acceptance.
Claims And Evidence: The authors provide theoretical justification (Proposition 2.1) showing that their state modelling objective equals the DecPOMDP objective. They perform extensive experiments on three benchmark environments (MPE, LBF, and RWARE) against multiple baselines with results that agree with their claims.
Methods And Evaluation Criteria: The evaluation metric (unnormalized average episodic reward) is common. The authors report results with confidence intervals averaged over six random seeds, which is sufficient for statistical significance. I appreciate not doing mean and standard error. The authors also properly analyze their method through ablation studies to verify the contribution of each component.
Theoretical Claims: The authors refer the proof to Proposition 2.1 as “missing proof”. I am not sure what that entails. The proof is sound and follows from the fact that the set of policies encompassed by the state modelling framework includes all policies that could solve the original problem. However, I am not familiar with this methodology.
Experimental Designs Or Analyses: The experimental designs and analyses appear sound. The authors use established benchmarks with appropriate configurations and metrics. The ablation studies are well-designed to isolate the contributions of different components.
One concern I have is that some figures show inconclusive results. A more detailed analysis in the style of rliable [1] could be more informative than some subfigures in Fig 3 and 4.
One minor concern is that the evaluation in MPE Spread with increasing number of agents (3, 4, 5, 8) doesn't fully demonstrate the scalability of the approach with even larger numbers of agents.
[1] Agarwal et al, Deep Reinforcement Learning at the Edge of the Statistical Precipice
Supplementary Material: I reviewed the supplementary material, which includes:
- Extended related work
- Additional experimental results on MPE
- Extended preliminaries on MAA2C and MLIAM
- The proof of Proposition 2.1
- Extended experimental setup with benchmark details
- Extended ablations
- t-SNE analysis
- Algorithm pseudocode
The supplementary material provides comprehensive information to understand and potentially reproduce the experiments.
Relation To Broader Scientific Literature: The state modelling framework extends previous agent modelling approaches by learning representations with respect to policy optimization rather than as an auxiliary task. This addresses a limitation in previous works such as "Agent modelling under partial observability for deep reinforcement learning" (Papoudakis et al., 2021) where the aim is to learn a relationship between the trajectory of the controlled agent and the modelled agent. The paper also suggests the use of adversarial methods.
The use of AM filters to handle redundant state information is motivated by findings in "Efficient multi-agent communication via self-supervised information aggregation" (Guan et al., 2022) where the authors aggregate the information through an attention mechanism. Note that the authors mention the same work twice for no reason as two separate entries.
The adversarial exploration schema uses hashing as done in "# exploration: A study of count-based exploration for deep reinforcement learning" (Tang et al., 2017), but applies it in a novel way to the multi-agent setting. I really like the paper’s study of the smoothness of the intrinsic reward smoothness rate.
Essential References Not Discussed: The paper appears to cover the most relevant related works in MARL, agent modelling, and exploration. However, it could benefit from discussing:
1. More recent work on belief representation learning in MARL, such as approaches using transformers or other sequence modeling techniques to handle partial observability.
2. More extensive comparison with world models or model-based MARL approaches
Other Strengths And Weaknesses: The paper is well-written with consistent notations and the clearly stated questions throughout the main body make the paper easy to follow. The formulas are clear and the notation is consistent. Figure 1 is not entirely clear and the arrow convention is not sufficient to distinguish the gradient and the data flow. This work could benefit a lot from more justification on how the baselines are selected, especially the ones that are fairly simpler than the proposed method.
The paper has a clear ablation study but I would like to see more details on how a method with this many components can scale up to more complex settings.
Other Comments Or Suggestions: 1. Check Figure 1 and more scalability analysis. Figure 3 and 4 have inconclusive results in some subfigures, it is very clear which ones.
2. Line 262 first column has a typo: “By doing do”
3. The Guan et al. paper is mentioned twice in the references. There is no need or reason.
4. Line 1194 should be *well-entagled* instead
Questions For Authors: 1. How does your method scale to more agents?
2. The choice of t_SNE seems somewhat arbitrary? Why choose that visualization over others? What additional observations can you make when using methods like PCA?
3. Are all the timesteps pooled together for the classification or is the accuracy reported for each timestep separately?
4. Along that line, it would be very interesting if you could show more in-between steps for the visualization. The timestep 45 makes sense but it can also come across as **cherry-picked**
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate your time and input, along with the positive evaluation. We respond to your comments and questions below.
> 1. A more detailed analysis in the style of rliable [42] could be more informative than some subfigures in Fig 3 and 4.
Thanks for this comment. We will consider using rliable in the camera-ready version.
> 2. Scalability with more agents
Regarding the scalability of our algorithm, Figure 2 shows that it clearly outperforms the other baselines in MPE Spread with 8 agents, albeit by a smaller margin compared to MPE Spread with 3, 4, and 5 agents. Furthermore, additional evaluations in LBF 8s-25x25-8p-5f and 7s-30x30-7p-4f (tasks have been benchmarked by the AAMAS2025 paper [1]) demonstrate that our algorithm achieves superior performance compared to the others.
|Env |SMPE |MAA2C |MAPPO|MASER|EOI|ATM
|-----------------:|---------:|--------:|----------:|----------:|------:|-----:|
| 8s-25x25-8p-5f| **0.64 +- 0.12**|0.52 +- 0.24|0.41 +- 0.23|0.01 +- 0| 0.07 +- 0.02 | 0.36 +- 0.28 |
| 7s-30x30-7p-4f| **0.74 +- 0.02**|0.71 +- 0.02 |0.57 +- 0.03|0.01 +- 0| 0.04 +- 0.01 | 0.59 +- 0.04 |
> 3. Comment on missing related works
Thank you for this comment. Does the reviewer some specific reference in mind? We will be happy to add missing related works.
> 4. Figure 1 is not entirely clear and the arrow convention is not sufficient to distinguish the gradient and the data flow.
Thank you for this comment. Our overview of SMPE^2 and the arrow convention follows a visualization approach similar to that of many well-established MARL papers (see [43], [44], [46]). If the reviewer still has objections about the figure, we are open to discuss possible improvements.
> 5. Justification on how the baselines are selected, especially the ones that are fairly simpler than the proposed method.
Our set of baselines includes some of the most well-known and relevant algorithms to ours. The choice of simpler algorithms was intentional, as MAA2C serves as the backbone of our algorithm, making it a natural baseline. Additionally, while MAPPO is a generalization of the single-agent PPO algorithm, it achieves strong results in our benchmarks, as described in [47].
> 6. The choice of t_SNE seems somewhat arbitrary?
We kindly disagree with this comment. t-SNE is a well established method used widely in the MARL community for embedding visualization (see [43],[44],[45]).
> 7. Are all the timesteps pooled together for the classification or is the accuracy reported for each timestep separately?
Thanks for this comment. Indeed all the timesteps pooled together for the classification.
> 8. The timestep 45 makes sense but it can also come across as cherry-picked
Thanks for this comment. The timestep 45 was not cherry-picked but selected on purpose to be at the end of the trajectory to represent the belief of each agent closer to the solution of the task. Furthermore in the Appendix E.4.8 we provide similar embedding visualizations for the timestep 30.
> 9. Note that the authors mention the same work twice for no reason as two separate entries. Line 262 first column has a typo: “By doing do”. The Guan et al. paper is mentioned twice in the references. Line 1194 should be well-entagled instead
Thanks for your comments. We will fix these minor typos.
**Due to space constraints, below we include responses to some of the questions of the other reviewers.**
> 10. Difference from LIAM, MAVEN and [3]
We respectfully disagree with the reviewer's comment.
- Regarding LIAM, please see lines 669-674. Also, note that LIAM does not use AM for exploration which is a major contribution of our paper.
- Regarding MAVEN, some clear differences are the following:
-- MAVEN does not account for non-informative state information which can be detrimental to MARL performance.
-- Our method is not based on committed exploration but on an adversarial competition among the agents, guided by z_i and a count-based method.
-- Our latent variables are not shared but are unique to each agent.
-- Our z_i is used as input to each agent's policy, rather than a component of the joint action-value function.
- Regarding [3], first of all, we believe that it is irrelevant as it solely considers single-agent RL, and thus it does not have to deal with MARL challenges, including multi-agent decentralized execution and non-stationarity. Additionally, [3] employs an intrinsic reward based on the prediction error of embeddings of pixel-based states, aiming to identify novel pixels. In stark contrast, we use a count-based hashing method on the belief z_i, which is informative of the unobserved state and policy optimization, ultimately improving joint exploration.
[3] Pathak, Deepak, et al. "Curiosity-driven exploration by self-supervised prediction". 2017.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed response.
> We kindly disagree with this comment. t-SNE is a well established method used widely in the MARL community for embedding visualization (see [43],[44],[45]).
This is a minor point but the papers mentioned do not use t-SNE. I am assuming that you are referring to [43][44][45] in your manuscript.
> Thanks for this comment. The timestep 45 was not cherry-picked but selected on purpose to be at the end of the trajectory to represent the belief of each agent closer to the solution of the task. Furthermore in the Appendix E.4.8 we provide similar embedding visualizations for the timestep 30.
I strongly bleieve the paper would benefit more from a wider sampling of which timesteps to visualize, e.g. including ealier and later steps.
---
Reply to Comment 1.1.1:
Comment: We would like to thank the reviewer for responding to our rebuttal.
Regarding the references, the reviewer is right. The references that use t-SNE visualization in MARL are (42; 59; 26) (as we also mention in Line 426 left). We apolozige for this confusion.
Regarding more timesteps to visualize, we will make sure to include more t-SNE figures in the camera-ready version of our paper.
Kind regards,
The authors
### References
[26] Liu, Z., Wan, L., Yang, X., Chen, Z., Chen, X., and Lan, X. Imagine, initialize, and explore: An effective exploration method in multi-agent reinforcement learning. In Proceedings of the AAAI Conference on Artificial Intelligence, volume 38, pp. 17487–17495, 2024
[42] Papoudakis, G., Christianos, F., and Albrecht, S. Agent modelling under partial observability for deep reinforcement learning. Advances in Neural Information Processing Systems, 34:19210–19222, 2021.
[59] Xu, P., Zhang, J., Yin, Q., Yu, C., Yang, Y., and Huang, K. Subspace-aware exploration for sparsereward multi-agent tasks. In Proceedings of the AAAI Conference on Artificial Intelligence, volume 37, pp. 11717–11725, 2023. | null | null | null | null |
Robot-Gated Interactive Imitation Learning with Adaptive Intervention Mechanism | Accept (poster) | Summary: The paper proposes an adaptive intervention strategy aiming to use the shared automony to improve the robot execution process. Previous robot -gated designs rely on the entropy to judge whether to let the human intervent. Using this strategy, the robot would frequently ask humans for the help, whihch is constly. Authors propose an a adaptie interactive intervention straetey, where Q function is learned, whch is further used to judge when to interact. Experiments demonstrated the effectiveness enabled by the method.
Claims And Evidence: The claims made are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The method and evaluation criteria make sense for the problem.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Experiemtnal designs are reasonalbe but a little bit simple.
The experiments mainly focus on evaluating the performance evolution of the agent as the number of human-involved steps increases. By comparing with previous robot-gated and human-gated imitation learning methods, authors wish to demonstrate that their method can achieve higher performance in a shorter time with fewer human-invovled steps. They also demonstrate that their method can help the agent receive sufficient human guidance at safety-critical issues.
The effectiveness of the proposed method can be validated by quantitative results shown in the table and plots. The main limitation lies in the simplicity of their evaluated tasks. Besides, qualitative evaluations are missing.
Supplementary Material: No supp. is submitted.
Relation To Broader Scientific Literature: Related to the robotics and adaptive policies.
Essential References Not Discussed: References are properly discussed.
Other Strengths And Weaknesses: Strengths:
- The motivating example in the method section is a good point and can help readers understand the problem setting and motivations.
Weaknesses:
- Line 053: "so the agent keeps requesting help at a fixed rate even when it has..." why "fixed intervention criterion" would cause "fixed request rate"? The logic between such two sentences is not clear.
- Line 071: "Second, our learned intervention criterion dynamically adjusts to the frequently changing agent policy during training." The meaning of this sentence is also unclear. What do you mean by "dynamically adjusts to...agent policy"? That's quite confusing.
- Line 295: "evaluation performance"? That's strange. "we report the success rate" or "we employ the success rate as the evaluation metric" would be better
Other Comments Or Suggestions: N/A
Questions For Authors: - Effecitveness in more complex tasks: Could the authors demonstrate the value of their method in more complex tasks such as those involving physical environments, e.g. Mojoco tasks like Ant in Gymnasium.
- Method design: why the proposed Q function could help the agent receive sufficient human guidance at "safety-critical states"? Why the Q-function can emphasize the "safety-critical states"?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your effort to thoroughly review our paper and for your feedback. In response to your feedback, we have included qualitative evaluations and ablation studies that have strengthened the study.
__Experimental Designs Or Analyses:__
>1.Qualitative evaluations are missing.
We include qualitative evaluations in Fig 1 of https://limewire.com/d/teXVP#Okg7PsYIne to show that when the car approaches the road boundaries, AIM successfully requests human intervention, while other uncertainty-based methods output a low uncertainty estimate and fail to signal the need for help.
__Other Strengths And Weaknesses:__
>1.Line 053: why "fixed intervention criterion" would cause "fixed request rate"? The logic between such two sentences is not clear.
In Line 053, __fixed intervention criterion__ refers to requesting human help when the __uncertainty estimate exceeds a constant $\epsilon$__, as in EnsembleDAgger, which uses the variance of actions in the policy ensemble as the uncertainty estimate.
According to Fig 4 of https://limewire.com/d/teXVP#Okg7PsYIne, __EnsembleDAgger requests expert help at a fixed intervention rate__ after 1K steps, implying that some states’ uncertainty estimates always exceed $\epsilon$. In contrast, ThriftyDAgger adapts $\epsilon$ and avoids a fixed request rate.
Therefore, we __revise Line 053__ as follows:
"The uncertainty-based methods including (Menda et al., 2019; Kelly et al., 2019) request human help when __the uncertainty estimate is larger than a fixed threshold__. __Without adjusting the threshold adaptively__, the agent keeps requesting expert help even when it has successfully imitated the human expert."
>2.Line 071: What do you mean by "dynamically adjusts to...agent policy"? That's quite confusing.
We __revise Line 071__ for clarity:
"Our learned intervention criterion adaptively __shrinks the intervention rate as the agent becomes performing__. Our learned intervention criterion can request human help at an appropriate rate based on the agent's performance during training."
We further explain Line 071 as follows. According to Line 184-188, the __intervention frequency of AIM gradually drops down__ as the agent’s performance improves during training. The reason is that AIM’s Q value depends on the proportion of states that the agent’s action aligns with the expert’s action. During training, the average of AIM’s Q value decreases towards -1, leading to the shrink of the intervention rate. The shrink of the intervention rate is also shown in Fig 4 of https://limewire.com/d/teXVP#Okg7PsYIne . We can observe that our method’s intervention rate matches that of human-gated PVP even though it’s a __robot-gated__ method, implying that our intervention mechanism adapts to the agent’s performance and resembles the human-gated intervention rule. In addition, our intervention rate is lower than other robot-gated baselines.
>3.Line 295: "we report the success rate" or "we employ the success rate as the evaluation metric" would be better.
Thanks for your suggestion! We revise Line 295 as follows:
"In MiniGrid, we employ the success rate as the agent’s evaluation metric."
__Questions For Authors:__
>1. Could the authors demonstrate the value of their method in more complex tasks such as those involving physical environments, e.g. Mujoco tasks like Ant in Gymnasium.
We appreciate the reviewer’s interest in evaluating our method on physical tasks such as those in MuJoCo. However, tuning and training a near-optimal expert and all baseline methods demand time and resources. Moreover, human demonstrations for MuJoCo tasks like Ant are infeasible, as a human cannot reasonably demonstrate the complex multi-legged locomotion task. Our MetaDrive environment with a high-dimensional observation space generates diverse driving scenarios such as fixed or movable traffic vehicles, traffic cones, and warning triangles, which already offers a compelling and challenging benchmark. We plan to include experiments on physical tasks in future work.
>2. Why the proposed Q function could help the agent receive sufficient human guidance at "safety-critical states"? Why the Q-function can emphasize the "safety-critical states"?
The key is that the proposed Q-function can classify states where __the agent’s actions align with human actions__ and those where __there is a significant action discrepancy__.
By explicitly using an action difference function $f$ to label these states, the Q-function learns to emphasize those states where human guidance is most needed. Additionally, incorporating a TD loss propagates these signals to nearby states.
We also include an ablation study in Fig 3 of https://limewire.com/d/teXVP#Okg7PsYIne , showing that dropping the TD loss or replacing the Q-labeling by reward-labeling will damage the performance of AIM. This implies the effectiveness of our AIM Q-function design. | Summary: This paper develops an approach to imitation learning called Adaptive Intervention Mechanism (AIM) that learns whether to ask an expert for an action label based upon whether AIM thinks the imitation learner already knows the correct action. An objective function is developed (Equation 3) that governs this AIM scheme by learning the weights of a Q-function, weighted by the level of disagreement between the expert and learner. Results are generated on some simple benchmarks and show that the proposed approach generally outperforms some baselines.
### Update after rebuttal
The reviewer appreciates the authors’ response and responded below. Overall, the response from the authors suggests a plan to improve the paper that would indeed improve the contribution to ICML. However, it would have been helpful to actually see these changes and have more details to ensure that the paper's claims match its contribtuions. I was initially a weak accept, and the rebuttal has solidified that rating for me.
Claims And Evidence: The claims that AIM is a novel algorithm, that the algorithm was evaluated and showed positive results is generally accurate. However, the term "sufficient" in the third claim (Line 98) should be softened unless providing a proof.
Methods And Evaluation Criteria: Yes, generally speaking, the approach and how it is evaluated make sense. However, a user study would have been helpful. There are issues described below.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The experimental design has a key weakness that it lacks a user study. Some of the results appear mixed (e.g., Figures 4-5). However, the analysis is reasonable for an ICML paper.
Supplementary Material: None provided.
Relation To Broader Scientific Literature: Except for the issue noted below regarding Confidence-based Autonomy, the paper generally covers the recent literature in interactive machine learning for an ML audience. However, the awareness of human-centered literature and decades of work on this topic seems to be lacking. I recommend more thoroughly reading the paper's own references, such as
Argall, B. D., Chernova, S., Veloso, M., and Browning, B. A survey of robot learning from demonstration. Robotics and autonomous systems, 57(5):469–483, 2009.
More recent papers/books might also help:
Esmaeil Seraj, Kin Man Lee, Zulfiqar Zaidi, Qingyu Xiao, Zhaoxin Li, Arthur Nascimento, Sanne van Waveren, Pradyumna Tambwekar, Rohan Paleja, Devleena Das and Matthew Gombolay (2024), "Interactive and Explainable Robot Learning: A Comprehensive Review", Foundations and Trends® in Robotics: Vol. 12: No. 2-3, pp 75-349. http://dx.doi.org/10.1561/2300000081
Ravichandar, H., Polydoros, A.S., Chernova, S. and Billard, A., 2020. Recent advances in robot learning from demonstration. Annual review of control, robotics, and autonomous systems, 3(1), pp.297-330.
Zare, M., Kebria, P.M., Khosravi, A. and Nahavandi, S., 2024. A survey of imitation learning: Algorithms, recent developments, and challenges. IEEE Transactions on Cybernetics.
Essential References Not Discussed: The paper does not discuss Confidence-based Autonomy (CBA).
Chernova, S. and Veloso, M., 2009. Interactive policy learning through confidence-based autonomy. Journal of Artificial Intelligence Research, 34, pp.1-25.
This paper sets up essentially the same problem and an analogous solution approach. There is an imitation learner that decides when to ask humans to take over control (add labels) vs. to autonomous execute (which still allows humans to observe and manually override). While Chernova's work was based upon a measure of model uncertainty (confidence), it is still directly related to how this paper uses a Q-function (albeit one I am confused about -- see my question regarding whether a TD-error actually means anything or exists). At a minimum, this prior work must be discussed, and the authors should do a more thorough literature review to find related papers that they might have missed by focusing only on recent trends in gated DAgger-like approaches. Ideally, this paper would benchmark against CBA.
Other Strengths And Weaknesses: Imitation Learning is, by definition [Ross et al., 2011], interactive and online. Humans give labels in real-time based upon online policy rollouts. The notion of "interactive imitation learning" seems to be confusing established concepts. The paper does provide references (such as Kelly et al., 2019) to back up this terminology, but I think it is unhelpful. If this paper refers to "imitation learning" in the sense of any learning from demonstration algorithm (whether it be Behavior Cloning or Inverse Reinforcement Learning (IRL)), then that needs to be clearer. Also, IRL is non-interactive but online. There is also offline IRL, etc. I think a more wholistic view of the literature and reaching further back into established concepts would improve the paper. I'd also refer the authors to this book [Chernova & Thomaz, 2022], which is a helpful treatise to define these concepts.
Ross, S., Gordon, G. and Bagnell, D., 2011, June. A reduction of imitation learning and structured prediction to no-regret online learning. In Proceedings of the fourteenth international conference on artificial intelligence and statistics (pp. 627-635). JMLR Workshop and Conference Proceedings.
Chernova, S. and Thomaz, A.L., 2022. Robot learning from human teachers. Springer Nature.
As per Lines 275-278, the paper says, "Following the prior works on interactive imitation learning (Hejna et al., 2023; Peng et al., 2021), we incorporate well-trained neural policies in the training loop to approximate human policies."
However, the limitations section is quite short and does not fully address the many weaknesses of not doing a real user study. Users are not "perfect," so claims should be softened.
Figures 4-5 show unconvincing results regarding the superiority of AIM vs. PVP.
It would have been helpful to include Adversarial Inverse Reinforcement Learning or a more competitive baseline. AIM requires online interaction with the user and the environment. AIRL may do quite well if given access to the environment but only limited data.
Other Comments Or Suggestions: There is a missing article in "mimic human intervention rule"
Questions For Authors: Under what conditions of f in Equation 2 is the agent able to recover the expert policy? Must it conform to the equation embedded in the text from Menda et al., 2019 and Hoque et al., 2021a;b? This claim seems to strong without offering further proof, and the description should be clearer if the authors are relying on prior work for the proof.
It is confusing to say that $Q^I_{\theta}(s, a_r)$ is equal to -1 or +1 by assignment (Lines 209-218). Should it not be the reward function definition for -1 and +1 -- not the Q-function? If it truly is the Q-function, then that implies that \gamma = 0 and Equation 4 is meaningless -- there is no TD-Error. Can the authors kindly clarify?
It is unclear how this paper is presenting an approach to "shared autonomy." See this work by Reddy et al. (2018).
Reddy, S., Dragan, A.D. and Levine, S., 2018. Shared autonomy via deep reinforcement learning. arXiv preprint arXiv:1802.01744.
Why are none of the baselines able to match the Neural Expert?
Why is the neural expert not at near 100% performance?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for reading our paper in detail and providing valuable suggestions. We summarize and respond to each question as follows:
__Claims And Evidence:__
>However, the term "sufficient" in the third claim (Line 98) should be softened unless providing a proof.
We revise Line 98: “The expert demonstrations requested by AIM contain corrective actions in safety-critical states, so that they can assist a novice agent to imitate the expert’s policy.”
__Relation To Broader Scientific Literature:__
>The awareness of human-centered literature and decades of work on this topic seems to be lacking. The paper does not discuss Confidence-based Autonomy (CBA).
Thanks for sharing relevant works! We will add these references in the revised version.
__Other Strengths And Weaknesses:__
>The limitations section is quite short and does not fully address the many weaknesses of not doing a real user study.
We will add this to the limitation section: "This paper does not include real-human experiments or user studies, and human demonstrations may be imperfect or faulty."
>Figures 4-5 show unconvincing results regarding the superiority of AIM vs. PVP.
Figures 4 and 5 show that AIM and PVP perform similarly in imitating the expert during safety-critical states and collect high-quality expert demonstrations. In short, __AIM’s intervention rule behaves similarly with the human-gated PVP’s rule, even though AIM is a robot-gated interactive IL method.__
In Figure 4 and 5, we do __not aim to show that AIM’s intervention rule is better than PVP__. According to Line 358-362 in Page 7, since PVP is a human-gated IL algorithm, the key advantage of AIM over PVP is that it requires fewer human cognitive efforts and expert-involved steps.
__Questions for Authors:__
>Under what conditions of f in Equation 2 is the agent able to recover the expert policy?
We clarify in Line 164 (Page 3) that the expert’s intervention method follows Eq. 2:
$I^{exp}(s, a_r, a_h) = f(a_r, a_h) = \mathbb{I}[\|a_r - a_h\|^2 > \epsilon]$ ($a_r$ is the robot action, $a_h$ is the human action). With sufficient expert demonstrations, we can bound the difference of the value functions of the expert policy and the student’s final learned policy by $\epsilon$ and the horizon $H$.
>Must the f in Equation 2 conform to the equation embedded in the text from Menda et al., 2019 and Hoque et al., 2021a;b?
The function f does not need to conform to Menda et al. (2019) and Hoque et al. (2021). The general form of the intervention is based on the probability of the expert taking the robot’s action, which reduces to Eq. 2 if the expert follows a Gaussian policy. The proof is in Theorem 3.3 of “Guarded Policy Optimization with Imperfect Online Demonstrations” (Z Xue et al., 2023).
>It is confusing to say that $Q_{\theta}^I(s, a_r)$ is equal to -1 or +1 by assignment (Lines 209-218). That implies that \gamma = 0 and Equation 4 is meaningless -- there is no TD-Error.
In Line 209-218, the proxy value assignment is a learning objective but not a hard constraint to the proxy value function. The AIM loss helps select human preferable actions at those states $s$ with human interventions, and TD loss propagates human preference to the states $s$ __without human interventions__.
>Should it not be the reward function definition for -1 and +1 -- not the Q-function?
We include an ablation study in Fig. 3 of https://limewire.com/d/teXVP#Okg7PsYIne . The figure shows that dropping the TD loss or replacing the Q-labeling by reward-labeling will damage the performance of AIM.
Replacing the Q-labeling by reward-labeling fails in our setting because negative rewards cannot be matched with transitions from unsafe agent actions. In human-involved transitions $(s, a_h, s’)$, we can assign +1 since $s’ \sim P(s, a_h)$ is generated by the human action. However, for dangerous agent actions $a_r$, querying the environment to obtain the resulting state $s’’ \sim P(s, a_r)$ is not feasible.
>It is unclear how this paper is presenting an approach to "shared autonomy." See this work by Reddy et al. (2018).
Thanks for pointing out that our definition of "shared autonomy" differs from Reddy et al. (2018), and we revise the terminology to "__interactive imitation learning__." While Reddy et al. apply human-AI shared control during both training and testing, we only use it in the training phase and evaluate the agent's performance without human involvement in the test phase.
>Why are none of the baselines able to match the Neural Expert?
In Table 1, we require all the baselines to use no more than 2K expert-involved steps. These baselines can match the neural expert with 3.5K expert-involved steps. See Fig 2 of https://limewire.com/d/teXVP#Okg7PsYIne .
>Why is the neural expert not at near 100% performance?
The neural expert is trained using Lagrangian PPO with 20M environment steps. MetaDrive safety environments can present challenging scenarios where a well-trained expert may fail.
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Rebuttal Comment 1.1:
Comment: The reviewer appreciates the authors’ response. The clarifications regarding the role of the proxy Q-function and how AIM differs from human-gated methods like PVP, as well as the explanation for why the neural expert does not reach near-perfect performance and why the baselines underperform under constrained expert involvement, were all helpful.
The authors' plan to soften the original claim about sufficiency and expand the discussion of prior work, especially with respect to Confidence-Based Autonomy and other foundational literature, is important. The acknowledgment of the limitations around the lack of user studies is a welcome addition. It would have been helpful to see this revision in the actual paper, but ICML does not allow for that.
The decision to revise the use of “shared autonomy” to more accurately reflect the scope of the work would improve the paper.
---
Reply to Comment 1.1.1:
Comment: Thanks again for your thoughtful feedback and constructive suggestions. We will follow your feedback to revise the paper accordingly, especially in adjusting the original claim on sufficiency, enhancing the literature review, and addressing the limitations related to user studies. | Summary: The authors proposed Adaptive Intervention Mechanism (AIM), a new robot-gated shared autonomy mechanism that better align agent with human expert thorugh a proxy Q-function. This algorithm requires less human monitoring comparing to human-gated interactive imitation learning methods, while more intelligently and efficiently request human expert intervention comparing to other robot-gated imitation learning methods. The authors tested the algorithms on MetaDrive and MiniGrid Four Room Test and achieved SOTA performance.
Claims And Evidence: See bullet points.
Methods And Evaluation Criteria: See bullet points.
Theoretical Claims: See bullet points.
Experimental Designs Or Analyses: See bullet points.
Supplementary Material: N/A
Relation To Broader Scientific Literature: Clear literature review.
Essential References Not Discussed: See bullet points.
Other Strengths And Weaknesses: 1. Why L2 distance instead of other distance metrics, for example distributional divergence for action-difference function f? It’s not very clear that in human demonstration data, in same state, a_{h} is unique and deterministic? Especially in task like MetaDrive?
2. Could the authors elaborate more on the choice of fixing the threshold epsilon in (9), I would be interested in knowing if an adaptive switch-to-agent threshold would work and perform even better, or if not better, what could be the reason.
3. Like the clear illustration in figure 2, could the authors give several example under safety-critical states, where other baselines robot-gated IL baselines fail to request for human help but AIM did?
4. The experiments for the continuous action space environment and discrete action space environment seems not well-aligned. Why authors did not compare AIM with Ensemble-Dagger and Thrifty-Dagger for mini-grid?
5. In both table 1 and table 2, results show that AIM is not the one with least total data usage, which is fine, since this not the superior aspect of AIM the authors are claiming. However, in page 7 line 374, the authors are claiming AIM’s mechanism saves training time and the total environment data usage according to figure 4, I think it’s not a fair comparison. (AIM with low rate of requesting human intervention could lead to longer training time in some cases.) If comparing vertically in figure 4, using same amount of data, AIM has the least deviation in the critical states, then you should also limit the experiments in table 1 and 2 to same total data then compare the success rate.
6. Since the authors claim the AIM’s great performance origins from it’s adaptive mechanism, I think if would be helpful to add a direct visualization of how the intervention rate changes during the training/testing stage, whether the agent request fewer human intervention as the agent getting more proficient. This should also be compared with other methods.
7. Since AIM has a human-gated warm up stage, would there be a chance that introducing this warm up stage to Ensemble-DAgger and Thrifty-DAgger would also leads to better performance? Then authors argument would be weakened.
Other Comments Or Suggestions: 1. What’s I^{exp}? What’s delta? Though some explanation appears in very later part of the paper, the author should explain each term in the formula (1) in the following paragraph, in order to have a clear background knowledge for the readers.
2. What’s the unit of the y axis for the plots in figure 2? Probability of human taking over? And how is uncertainty estimated? It seems not quite reasonable that many steps come with 0 uncertainty. Would be great to add clear legends to help better explanation.
Questions For Authors: See bullet points.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for taking the time to carefully read through and understand our paper, and provide constructive feedback. We summarize and respond to each question as follows:
__Other Strengths And Weaknesses:__
>1.Why L2 distance instead of other distance metrics? Is $a_h$ unique and deterministic in task like MetaDrive?
We use L2 distance because it is simple to implement and effectively identifies states where the agent's actions deviate significantly from expert behavior. Fig 3 in https://limewire.com/d/teXVP#Okg7PsYIne shows that using the L1 distance metric does not affect the performance. In MetaDrive, the expert action $a_h$ is stochastic, as the expert policy is a stochastic policy trained with Lagrangian PPO.
>2.Elaborate more on the choice of fixing the threshold epsilon in Eq. 9.
The threshold $\epsilon$ controls __the length of expert demonstrations after the agent requests help__. We choose $\epsilon$ based on observations from the human replay buffer in warm-up steps (Eq. 8, Line 240). A small $\epsilon$ leads to overuse of expert help, while a large $\epsilon$ results in insufficient corrections, slowing down training.
>Does an adaptive switch-to-agent threshold work and perform better?
An adaptive switch-to-agent threshold does __not__ significantly improve the number of expert-involved steps. In our current setup, the agent requires only 5–10 steps of expert help before returning to self-exploration, which is nearly the minimum needed for safety.
>3.Give several examples under safety-critical states, where other baselines robot-gated IL baselines fail to request for human help but AIM did.
In Fig. 1 of https://limewire.com/d/teXVP#Okg7PsYIne , when the car approaches the road boundaries, AIM successfully requests human intervention, while other uncertainty-based methods output a low uncertainty estimate and fail to signal the need for help.
>4.Why did authors not compare AIM with Ensemble-Dagger and Thrifty-Dagger for mini-grid?
In Page 6 Line 310-314, we mentioned that the two methods rely on the action variance for uncertainty estimation, which doesn’t work well with __discrete action spaces__ like MiniGrid. 'Action variance' refers to the variance of the output actions across the ensemble of policy networks.
To apply the two baselines to MiniGrid, we need to replace their variance-based uncertainty estimations by the __entropy-based__ estimation, which is the entropy of the action distributions derived from the soft Q-value. Table 1 of https://limewire.com/d/teXVP#Okg7PsYIne shows that AIM reduces the expert-involved steps needed compared with the two baselines.
>5.In page 7 line 374, the authors are claiming AIM’s mechanism saves training time and the total environment data usage according to figure 4, but results show that AIM is not the one with least total data usage.
Thanks for pointing out the misleading claim. In Figure 4, we show that AIM requires fewer environment samples than other robot-gated baselines (Thrifty-DAgger and Ensemble-DAgger) to approach expert actions in safety-critical states. In Table 1 and Table 2, we highlight that AIM reduces expert-involved steps and cognitive effort, though it may require more training time. Thus, we revise line 374 to:
"Compared with __other robot-gated IIL baselines__, AIM requires fewer environment data usage to __imitate expert actions in safety-critical states__."
>6.How does the intervention rate change during the training/testing stage?
We visualize the overall intervention rate in the training stage in Fig. 4 of https://limewire.com/d/teXVP#Okg7PsYIne . Our method AIM’s intervention rate matches that of human-gated PVP and is lower than other robot-gated baselines.
According to Line 281-284, in the test stage, we evaluate the agent’s performance without expert involvement, so there’s no intervention rate during testing.
>7.Does introduce warm up stage to Ensemble/Thrifty-DAgger lead to better performance?
In our experiment (Table 1 and Table 2), we already introduced a warm up stage to all the baselines including Ensemble-DAgger, Thrifty-DAgger, and PVP for fairness. (i.e., demonstrating initial two trajectories as we do for AIM).
__Other Comments Or Suggestions:__
>1.What’s $I^{exp}$, $\delta$ in the formula (1)?
$I^{exp}$ is the human-gated intervention criterion, where the expert decides whether to take over control at state s using human control signal $a_h$ when the agent outputs action $a_r$. The $\delta$ function in Eq. 1 is the __Dirac delta distribution__.
>2.What’s the unit of the y axis for the plots in figure 2? How is uncertainty estimated?
In Figure 2, the y-axis represents the uncertainty estimation: $Var(a_n) - \varepsilon$, where $Var(a_n)$ is the variance of agent actions and $\varepsilon$ is the switch-to-human threshold in Ensemble-DAgger. Human help is requested when $Var(a_n) > \varepsilon$. We plot $\max(0, Var(a_n) - \varepsilon)$ to visualize the timesteps when human help is requested.
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Rebuttal Comment 1.1:
Comment: Thank the authors for the detailed response. I have raised my score to 3. | null | null | null | null | null | null | null | null |
A Rescaling-Invariant Lipschitz Bound Based on Path-Metrics for Modern ReLU Network Parameterizations | Accept (poster) | Summary: The paper proves a new reparameterization invariant Lipschitz bound in terms of the “path-metrics” of the parameters. The bound applies generally to network architectures with pooling and skip connections. Using the bound, the authors propose a rescaling-invariant pruning criterion.
Claims And Evidence: The authors claim that their bound is rescaling invariant, while it is theoretically sound due to the construction of path-lifting space, there is no experimental evidence that the bound is non-vacuous, e.g. both sides of the bound correlate with one another.
Line 311-315 left column: “We show this to match the accuracy of magnitude pruning when applied to ResNets trained on Imagenet in the lottery ticket context (Frankle et al., 2020), while being rescaling-invariant”. I cannot find any figures/tables that support this claim, except what is briefly mentioned in line 396-399.
Methods And Evaluation Criteria: There is no empirical evaluation.
Theoretical Claims: I have checked the proof sketch of theorem 3.1, and it looks sound to me.
Experimental Designs Or Analyses: There is little or no experimental result shown.
Supplementary Material: I skimmed through the supplementary material
Relation To Broader Scientific Literature: The authors claim that they are the first in literature that propose a scale invariant Lipschitz bound. I found the support for the usefulness of a Lipschitz bound weak in the paper, and only two papers are mentioned (Neyshabur et al., 2018; Gonon et al, 2023). Moreover, the Lipschitz bound in Neyshabur et al., 2018 is only used to bound sharpness, which in turn connects to generalization. On the sharpness side, there are plenty of rescaling invariant bound proposed since Dinh et al., 2017, and I feel that the authors should more thoroughly discuss this connection with sharpness bounds, and see how their bound is relevant. In fact, if MSE loss is used, sharpness is exactly the norm of gradient of the output of networks w.r.t. the parameters (see e.g. Wen et al., 2023, lemma 4.1; Ma & Ying, 2021, Equation 3).
Essential References Not Discussed: No work absolutely needs to be brought up. But I think work related to rescaling invariant sharpness is worth mentioning due to the reason above. Similarly, more work that shows the usefulness of a Lipschitz bound can be mentioned.
Other Strengths And Weaknesses: For the main inequality (3), if we have a normalization layer on the input (which is valid according to line 77), wouldn’t it make the inequality vacuous, since we can arbitrarily scale the input with R and \theta stays the same?
Other Comments Or Suggestions: No other comments.
Questions For Authors: No other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your review. We address your points below.
1. > what if there is a normalization layer on the input
We assume you refer to batch normalization. As detailed in Gonon et al. 2024, batch normalization layers *as they behave at inference* are indeed covered in the path-lifting framework. While at training batch normalization dynamically adapts its weights to batches, this is no longer the case at inference where it acts as a plain affine layer. As a result, *the problem you raise does not appear*. The revision will make it clear.
2. > mentioning the relation to sharpness
Sharpness measures [1, 2] are typically defined in terms of (averaged) loss differences $L(\theta+\delta) - L(\theta)$ over perturbations $\delta\in B(0,r)$ around a local minima $\theta$. As such, they are not rescaling-invariant measures of $\theta$ *alone*, since rescaling only $\theta$ but not the perturbation $\delta$ will change this quantity in general. *One* consequence of our main Theorem 3.1 is to further bound this type of sharpness measure (again by something which is not invariant in $\theta$ alone, but invariant in both $\delta,\theta$). Indeed, if $L(\theta) = \sum_{i=1}^n \ell(R_{\theta}(x_i), y_i)$ with $\ell$ Lipschitz in its first argument (e.g., cross-entropy, or squared loss on a compact), it holds $\|\ell(R_{\theta+\delta}(x_i), y_i) - \ell(R_{\theta}(x_i), y_i)\| \leq c \|\|R_{\theta+\delta}(x_i) - R_{\theta}(x_i)\|\|$ and the latter is bounded by $c \|x_i\| \|\|\Phi(\theta+\delta) - \Phi(\theta)\|\|$ according to Theorem 3.1.
We will add this to the final version.
3. > I found the support for the usefulness of a Lipschitz bound weak in the paper
If we understood correctly, you are asking about the usefulness of Lipschitz bounds beyond their use to bound sharpness as above. The revision will cite additional papers [3-9] that use *non-invariant* Lipschitz bounds of the same type as those in (Neyshabur et al., 2018; Gonon et al, 2023) to design new algorithms and guarantees on pruning, quantization and generalization (not through sharpness, but via covering numbers). In all of these papers, Lipschitzness comes in as a crucial property to control how the function changes with small weight perturbations. However, these papers unfortunately suffer from the two problems motivating our paper: 1) they use non-invariant bounds, which not only can be made arbitrarily pessimistic but that might also yield algorithms with huge performance drops when run on rescaling-equivalent parameters (Figure 6), and 2) they only hold for simple fully-connected models organized in layers.
[1] How Does Sharpness-Aware Minimization Minimize Sharpness? Wen et al. 2023. Table 1.
[2] A Modern Look at the Relationship between Sharpness and Generalization. Andriushchenko et al. 2023. Equation (1).
[3] Liebenwein et al., Provable Filter Pruning for Efficient Neural Networks, ICLR 2020.
[4] Baykal et al., Data-dependent Coresets for Compressing Neural Networks with Applications to Generalization Bounds, ICLR 2019.
[5] SiPPing Neural Networks: Sensitivity-informed Provable Pruning of Neural Networks. Baykal et al. 2019.
[6] Arora et al., Stronger Generalization Bounds for Deep Nets via a Compression Approach, ICML 2018.
[7] Zhang et al., Post-training Quantization for Neural Networks with Provable Guarantees, 2023.
[8] Lybrand and Saab, A Greedy Algorithm for Quantizing Neural Networks, JMLR 2021.
[9] Schnoor et al., Generalization Error Bounds for Iterative Recovery Algorithms Unfolded as Neural Networks, 2022.
---
Rebuttal Comment 1.1:
Comment: I meant layer normalization. I see that you wrote batch normalization instead, so maybe it does not apply to your setting.
[2] above uses rescaling invariant sharpness measure and is invariant under multiplicative reparametrizations. The explanation immediately follows equation (1) therein. I don't understand why the authors say otherwise.
There are many scale invariant definitions of sharpness:
1. Tsuzuku, Y., Sato, I., and Sugiyama, M. Normalized flat minima: Exploring scale invariant definition of flat minima for neural networks using pac-bayesian analysis,2019.
2.Kwon, J., Kim, J., Park, H., and Choi, I. K. Asam: Adaptive
sharpness-aware minimization for scale-invariant learning of deep neural networks. In International Conference
on Machine Learning, pp. 5905–5914. PMLR, 2021. (Used in [2])
3.Rangamani, Akshay, et al. "A scale invariant flatness measure for deep network minima." arXiv preprint arXiv:1902.02434 (2019).
I lean towards rejection also because there is no proper exhibition of experimental results in the main text, and no comparison to other pruning methods. All I see in the main text is Table 3, which shows the computing time for the pruning methods. The authors should put Table 4 and Figure 6 in the main text.
Also, the pruning method is not a direct evaluation of how tight the bound in theorem 3.1 is. The authors should evaluate both sides of the inequality to see if the inequality is useful.
---
Reply to Comment 1.1.1:
Comment: **Layer normalization**: indeed, normalization layers are not rescaling-invariant, and as such are not covered by the path-lifting framework, unlike batch normalization layers.
**Experimental results in the main text**: in the final version we can group existing figures to gain space and move relevant aspects of appendix D to the main text to complete Table 3.
**Rescaling-invariant sharpness measures**: indeed we based our answer on the definition of sharpness from [1] and missed the adaptiveness allowed by the additional vector $c$ from [2] and the other references you point out, which yield rescaling-invariant measures, thank you.
**Pros and cons of the proposed Lipschitz bound**: Table 2 summarizes key properties of various pruning criteria including the one directly derived from our Lipschitz bound. A similar table can be carved out for other potential applications of the bound such as sharpness measures. We will include it to highlight the pros and cons of the bound: while the pruning criteria and sharpness measures derived from it may be legitimately criticized for their potential numerical sub-optimality for such or such application, one of the main strengths of the bound (beyond its generic rescaling invariance) is also its flexible applicability to diverse settings, thanks to its independence from a particular dataset or a particular loss. | Summary: The paper derives a Lipschitz upper bound for neural networks with ReLU and k-max-pooling activations. For two parameters $\Theta$ and $\Theta'$, the paper shows that $||R_{\Theta}(x)-R_{\Theta'}(x)||_1\leq max(||x||_∞,1) ||\Phi(\Theta)-\Phi(\Theta')||_1$, with an assumption that $\mathrm{sign}(\Theta)=\mathrm{sign}(\Theta')$.
Here the new vector $\Phi(\Theta)$ is the lifting of the original parameter $\Theta$. This upper bound is rescaling-invariant, meaning that the upper bound only relies on the intrinsic property of the network, instead of the parameter. For any two parameters $\Theta_1$ and $\Theta_2$ such that $R_{\Theta_1}=R_{\Theta_2}$, then their liftings $\Phi(\Theta_1)=\Phi(\Theta_2)$.
This inequality can be used to prune a dense network into a sparse one, while ensuring it has similar performance compared with the dense network.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes, the proof of the main theorem 3.1 is correct
Experimental Designs Or Analyses: Didn't find any issue.
Supplementary Material: The proof part.
Relation To Broader Scientific Literature: It is a deep learning theory paper that might be useful for pruning.
Essential References Not Discussed: I didn't discover this issue.
Other Strengths And Weaknesses: Strength: The paper introduces a scaling invariant Lipschitz upper bound using parameter lifting. It is very clear and rigorous. The proof is well written.
Weakness: The main result theorem 3.1 in this paper seems quite simple. The generalization bound derived from this theorem is not clearly stated and proved. (I am actually curious about that.) This theorem 3.1 has an application in pruning, but I am not very certain whether this theorem can be very impactful in other applications.
Other Comments Or Suggestions: see 'Questions For Authors'.
Questions For Authors: 1. The assumption that $\mathrm{sign}(\Theta)=\mathrm{sign}(\Theta')$ seems very strong. If we no longer assume this, is it possible to derive a looser upper bound? If we assume there are only a few edges $i$ such that the weights $\Theta_i\Theta'_i<0$, what bound can you get?
2. Without requiring rescaling invariance, is it possible to extend the activation to leaky ReLU or some smooth activation functions? In that case, what is your upper bound?
3. Is it possible that when the network is very deep and over-parameterized, the output of the network $R_{\Theta}(x)$ is small, but every entry in your lifting $\Phi(\Theta)$ is very large ($\Phi_p(\Theta)\gg0$), so you do not get a meaningful bound when you do pruning using equation (13)? In this case, is it possible to do some pruning while ensuring the output $R_{\Theta}(x)$ doesn't change much?
I will adjust the rating based on the answers and also the comments from other reviewers.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review. We address your points below.
1. > assumption of sign consistency and extension to cases where only a few edges have different signs?
As shown by the example in Figure 5, page 13 (that we will move to the main text), the sign assumption cannot be simply removed in Theorem 3.1. This is thus not a limitation of the approach but a limitation of the achievable Lipschitz bound. We will highlight this fact, which is indeed a contribution. It is not difficult to design variants of the counterexample of Figure 5 with network parameters sharing the same sign on every edge except two, by "prepending" and "appending" arbitrary networks to the example.
Besides, we highlight that this is not a limitation in practice for applications even beyond pruning (for example quantization), and it allows one to obtain generalization bounds with *free* signs (the proof sketch is given line 202, and could certainly be detailed in the supplementary in the final version if requested).
2. extension to networks with activations beyond the ReLU
The leaky ReLU remains rescaling invariant and piecewise linear. Although the current path-lifting framework used to derive Theorem 3.1 does not cover the leaky ReLU, it is possible that a complete re-examination of this framework might allow for a generalisation of Theorem 3.1 to this activation. Regarding non rescaling-invariant activations, we cannot expect any bound of the same type as in Theorem 3.1 to directly hold as the right-hand-side is rescaling invariant.
3. meaningful bound when deep/overparameterized networks, as path-coefficients are large
You are perfectly right: although the provided bound is the sharpest of its kind, it somehow remains a worst case over all weights with a prescribed path-norm. It now raises the challenge of obtaining tighter "average" bounds.
---
Rebuttal Comment 1.1:
Comment: I will adjust my rating after studying the comments from other reviewers carefully. | Summary: This paper introduces a novel Lipschitz bound for modern ReLU neural networks that is invariant under neuron-wise rescaling transformations. The key idea is to leverage a "path-lifting" function which transforms the network parameters into a high-dimensional path space, where each coordinate corresponds to the product of weights along a path. While the path‑lifting function and the associated path‑norm have been introduced in previous works [1], this paper extends these ideas by establishing a rescaling‐invariant Lipschitz bound and deriving a practical pruning criterion. In other words, it is not the tool itself that is new, but its effective integration into a Lipschitz analysis framework that remains invariant under neuron‐wise rescaling and its subsequent application.
And the paper further illustrates the utility of this invariant bound by deriving a new rescaling-invariant pruning criterion termed “Path-Magnitude Pruning,” and reports experiments demonstrating that this approach maintains performance under adversarial rescaling that would affect conventional magnitude pruning.
[1] Gonon, A., Brisebarre, N., Riccietti, E., & Gribonval, R. (2023). A path-norm toolkit for modern networks: consequences, promises and challenges. arXiv preprint arXiv:2310.01225.
## Update after rebuttal
- I thank the authors for their response, which generally resolved my concerns. I will maintain my Overall Recommendation for the manuscript, standing on the acceptance side.
Claims And Evidence: 1. Novel Lipschitz Bound and Rescaling-Invariance:
The paper introduces a new Lipschitz upper bound based on path-metrics that is invariant to neuron-wise rescaling. The authors provide mathematical proofs (e.g., Theorem 3.1 and supporting lemmas) demonstrating that, under the assumption that parameter pairs maintain the same sign, the derived bound is both tighter and robust compared to traditional bounds based on standard ℓₚ norms.
2. Path-Magnitude Pruning Criterion:
The paper proposes a pruning criterion (Path-Mag) derived from the proposed Lipschitz bound. The authors offer both an analytical justification (Lemma 4.2) and experimental results on ResNet-18 trained on ImageNet, demonstrating that the approach maintains performance under random rescaling—a scenario where conventional magnitude pruning fails.
3. The major limitation is the assumption of parameters. Although practically justifiable in many scenarios (e.g., during pruning or with small gradient steps), this condition restricts the generality of the claim. Additionally, empirical evidence is limited to a single network (ResNet-18), leaving some uncertainty about applicability to other architectures.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for obtaining a rescaling-invariant Lipschitz bound based on path-lifting functions.
Theoretical Claims: Overall, the proofs for the primary theoretical claims—including Theorem 3.1 (and its extensions) and the supporting lemmas—are correct and employ rigorous mathematical reasoning. The primary concern lies in the necessary assumption of sign consistency, which, although justifiable in many practical applications, narrows the scope of the theoretical claims. Furthermore, some steps in the proofs could benefit from enhanced clarity to assist readers less familiar with the underlying techniques.
Experimental Designs Or Analyses: The experimental design and analyses are valid and sufficiently support the theoretical claims. The approach is well-motivated and the comparative evaluation is clear, despite being limited to a single network architecture (ResNet-18) and lacking extensive hyperparameter exploration.
Supplementary Material: Yes, I have checked the supplementary Materials, including the numerical and
theoretical parts.
Relation To Broader Scientific Literature: This work contributes to the broader literature in several ways:
- **Theoretical Insight:** It builds on and extends prior work on the path-norm and Lipschitz analysis of neural networks (e.g., by Neyshabur et al., Gonon et al.).
- **Practical Applications:** The method provides a new tool for pruning and potentially quantization, addressing known issues with conventional parameter norm bounds.
- **General Applicability:** It successfully generalizes to modern network architectures that include pooling and skip connections, areas where traditional bounds are less effective.
Overall, the contribution is well situated within the existing literature on neural network generalization and robustness.
Essential References Not Discussed: I did not identify any major omissions of essential references. The manuscript appears to adequately cover the relevant literature.
Other Strengths And Weaknesses: ### Strengths
- **Innovative Theoretical Approach:**
The use of path-lifting to achieve a rescaling-invariant Lipschitz bound is a clever idea that addresses a long-standing limitation in norm-based bounds.
- **Broad Applicability:**
The theoretical results extend to modern network architectures beyond simple feedforward models, encompassing pooling layers and skip connections.
- **Practical Utility:**
The derived bound is directly applied to design a rescaling-invariant pruning method, and experimental results confirm its practical benefits.
### Weaknesses
- **Assumption Limitations:**
The theoretical guarantees require that corresponding parameters share the same sign, which might limit applicability in some practical settings.
- **Clarity in Presentation:**
There are some typos, for example, in Definition A.2, the definition of $\theta^{v\rightarrow}$ appears to be incorrect.
Other Comments Or Suggestions: - **Further Discussion on Assumptions:**
The authors should include more discussion on the practical impact of the sign consistency condition and potential extensions when this assumption is relaxed.
- **Enhanced Experimental Comparisons:**
It would be beneficial to include additional comparisons with other norm-based or invariance-aware methods, especially under diverse conditions of weight perturbation.
Questions For Authors: No other comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review. We address your points below.
1. > The major limitation is the assumption of parameters/assumption of sign consistency
As shown by the example in Figure 5, page 13 (that we will move to the main text), the sign assumption cannot be simply removed in Theorem 3.1. This is thus not a limitation of the approach but a limitation of the achievable Lipschitz bound. We will highlight this fact, which is indeed a contribution.
Besides, we highlight that this is not a limitation in practice for applications to quantization and pruning, and that it allows to obtain generalization bounds with *free* signs.
2. > limited empirical evidence
The pruning experiment on a ResNet-18 is intended to be a proof-of-concept illustration of *one* possible application of our main contribution, which is theoretical: the nontrivial proof of Theorem 3.1. To avoid unnecessary energy consumption, we voluntarily avoided extensive comparisons which are clearly out of the scope of our claimed research contribution. In fact, the code that we will release on a non-anonymous repository allows to apply the same approach to more than 37 architectures available on torch. | null | null | null | null | null | null | null | null |
Graph Diffusion for Robust Multi-Agent Coordination | Accept (spotlight poster) | Summary: This paper introduces MCGD (Multi-agent Coordination based on Graph Diffusion), which is a novel framework for offline multi-agent reinforcement learning (MARL) that aims to improve coordination effectiveness and robustness of the policies in dynamic environments. Specifically, MCGD uses graph to model the relationship and coordination of agents. When doing sampling, MCGD uses categorical diffusion to model discrete edge attributes (the correlation between agents) and use anisotropic diffusion to model continuous node attribute (actions of the agents). The authors conducted extensive experiments in different platforms to demonstrate the outstanding performance compared with benchmarks.
## Score updated after Rebuttal
Claims And Evidence: The authors claim that by using MCGD the coordination of agents can be improved especially in dynamic environments. To show this, in the introduction part of the paper, the authors mentioned the case where one agent suddenly becomes unavailable to demonstrate the importance of designing algorithms to tackle general dynamic environments. However, such environments are not tested in the experiments according to the shifted environments in appendix 7.4.2. It would be nice if the authors could have more experiments about changing the number of agents (agents become unavailable or adding new agents to the env) to demonstrate the capability of dealing with environmental changes.
Besides, the agent number of the experiments is greatly limited. In MPE envs, the number of agents is less than 10. Although the authors listed the sampling time comparison result when the number of agents varies from 8 to 64 in 7.5.2, but the planning performance of these experiments is not discussed. In order to better demonstrate the generalizability of the framework, experiments and planning performance comparison when the number of agents is different is beneficial.
Methods And Evaluation Criteria: The authors tested the proposed framework in multiple simulation platforms with benchmarks in different tasks, which is pretty comprehensive and clear. It would be better if more experiments, especially real world robotics experiments, can be included.
Theoretical Claims: The proofs look good to me.
Experimental Designs Or Analyses: See Claims And Evidence part of the review.
Supplementary Material: I reviewed the derivations and experiment details listed in the appendix. Relative questions are raised in other parts of the review.
Relation To Broader Scientific Literature: This paper studies the MARL problem, which is an important method in multi-agent motion planning. The proposed MCGD framework improves the coordination performance and robustness in dynamic environment, which is important for future real world applications and generalization to more practical scenarios.
Essential References Not Discussed: References look good to me.
Other Strengths And Weaknesses: The paper is written and organized clearly with useful illustrations and diagrams.
Other Comments Or Suggestions: See above.
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the constructive feedback. We have addressed all comments and revised the manuscript accordingly. Responses are organized by reviewer Weaknesses (W) and Questions (Q), with relevant figures and tables provided in the [anonymized supplementary material](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF).
$\bullet$ W1: Testing Environments with Dynamic Agent Numbers.
We would like to clarify that our original manuscript already includes evaluation in dynamic settings where agent availability changes.
Specifically, during testing on the MPE Spread task, we randomly selected one of the three agents and set its velocity to zero to simulate a sudden offline event.
The corresponding results are reported in the “Coordination Structure” column of Table 2.
We believe the confusion may stem from Appendix 7.4.2, which focuses on attribute variation (e.g., speed changes) rather than agent removal.
To further address your concern, we have extended our evaluation by increasing the number of agents and landmarks to 8.
During testing, we randomly deactivate 1 to 4 agents by setting their velocities to zero.
As shown in Table 4 of the anonymized supplementary material, MCGD consistently outperforms baselines such as DOM2 and MADIFF under all conditions.
Notably, the performance gap widens as more agents go offline, highlighting MCGD’s robustness and adaptability in highly dynamic environments.
These results support our claim that MCGD is well-suited for handling general coordination under dynamic agent configurations.
$\bullet$ W2: Scalability Comparison.
While our core experiments follow prior diffusion-based offline MARL settings [1-3], which typically involve fewer than 10 agents, this does not indicate a limitation of our framework in large-scale scenarios.
In Appendix 7.4.2, we first evaluate computational efficiency by comparing sampling time under increasing agent numbers (8 to 64).
Despite the added complexity of structural diffusion, MCGD remains competitive with existing baselines such as MADIFF.
To further assess planning performance at scale, we additionally conduct experiments on the MPE Spread task with 8, 16, 32, and 64 agents.
As reported in Table 1 of the anonymized supplementary material, MCGD consistently outperforms MADIFF and DOM2 across all settings, with the performance gap widening as the number of agents increases.
This trend highlights MCGD’s ability to effectively model complex collaboration patterns under growing agent populations.
These results confirm that our framework is not only computationally scalable, but also capable of maintaining strong coordination performance in large-scale environments.
$\bullet$ W3: Real World Applications:
We agree that real-world validation is an important direction to further demonstrate the practical applicability of our framework.
Our team is currently working on deploying the proposed method in real-world multi-robot hunting scenarios.
While we do not yet have quantitative results ready for inclusion in this version, we are actively collecting data and refining the deployment process.
We plan to report these findings as part of a more extensive evaluation in a future journal extension of this work.
References:
[1] Beyond Conservatism: Diffusion Policies in Offline Multi-agent Reinforcement Learning, Li et al, CoRR 2023.
[2] Madiff: Offline multi-agent learning with diffusion models, Zhu et al, NeurIPS 2024.
[3] Diffusion-based Episodes Augmentation for Offline Multi-Agent Reinforcement Learning, Oh et al, ICML 2024.
---
Rebuttal Comment 1.1:
Comment: Thank you for the authors' responses. The provided figures and tables look good to me and address my concerns.
I have one remaining follow-up question about W1. About the experiments with dynamic agent number, will "add more agents" be different? Indeed, setting and fixing speed to zero can simulate the case where some agents become offline in execution, but in many long-horizon tasks, especially in life-long execution cases, adding more agents will also be worth studying and interesting. Will this case be theoretically and empirically different than the existing experiments? If yes, could you analyze this case? If not, could you explain the reason?
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your insightful suggestion. We fully agree that dynamically adding agents during execution is an important and realistic setting, especially in life-long or open-ended multi-agent systems. In response, we have extended our experiments to include this scenario and carefully analyzed its impact on collaborative behavior.
Specifically, we designed a new experiment based on the MPE Spread task. In this setup, we fixed the number of landmarks to 4 while keeping the number of agents as 3 during training. During execution, however, we introduced an additional agent with a fixed policy to simulate the case of dynamically joining agents. The goal was to evaluate whether the original 3 agents, trained without the presence of this fourth agent, could adapt their strategies on-the-fly to maintain effective collaboration.
The quantitative results of this experiment are presented in Table 5 (see [anonymous link](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF)). Notably, our proposed method, MCGD, demonstrates superior collaboration robustness compared to baselines, both during training and under dynamic execution conditions. In particular, the performance gain upon adding the new agent during testing reaches 11.7%, highlighting MCGD's adaptability in dynamic multi-agent environments.
To further illustrate the cooperative behavior adjustment, we visualized the agent trajectories in both 3-agent and 4-agent execution settings (see Figure 2 in the [anonymous link](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF)). During training, due to the mismatch between the number of agents and landmarks, agents developed strategies that did not rely on strict 1-to-1 assignment. For instance, some agents learned to minimize the combined distance to two landmarks rather than commit to a single target.
In the dynamic execution phase, the newly added agent initially starts far from all landmarks, and thus the original 3 agents continue their learned behavior. However, as the new agent approaches a specific landmark, the other agents dynamically revise their goals, often yielding their original targets and reassigning themselves to the closest remaining landmarks. This behavior shift results in a significant performance boost and offers a clear demonstration of MCGD's robust cooperation under dynamic agent populations. | Summary: This paper introduces Multi-agent Coordination based on Graph Diffusion (MCGD), a novel framework for offline multi-agent reinforcement learning (MARL) that uses graph diffusion models to enhance coordination in dynamic environments. MCGD constructs a coordination graph to capture multi-agent interactions and uses a form of categorical and anisotropic diffusion processes to model agent interactions and actions. The framework outperforms existing state-of-the-art baselines in coordination performance and policy robustness across various multi-agent environments.
## update after rebuttal
I appreciate the additional experiments and hope any remaining corrections are fixed in the final version of the paper.
Claims And Evidence: The major claims are supported by results on a set of multi-agent benchmarks with off-the-shelf datasets. The graph diffusion model for multi-agent coordination using a graph transformer network appears novel.
However, the claim that the anisotropic diffusion process models the diversity in single agent actions is not adequately explored. “Diversity” could be quantified better (such as a metric based on mutual information [1] or SND [2]) and supported with experiments.
Methods And Evaluation Criteria: For categorical noising, a transition matrix (Eq. 6) is derived from the cosine similarity between agent observations. The intuition behind this formula is not readily apparent. An explanation could be a high similarity between agent observations implies a high value at $Q_{ij}$ meaning the agents are connected. The authors could further address the motivations of this transition matrix.
The continuous node attributes $A_t$ in graph $G_t = (A_t, E_t)$ are $d$ dimensional and encode the agent actions. It is unclear if this means it stores the actions of all agents (with a common dimension $d$) or is some form of action embedding. The method to extract an action for each agent from the predicted $\hat{A}^t$ is not obvious.
The Q-loss used in the anisotropic diffusion loss (Eq. 15) is not explained in the main body. For instance, how are the Q-values estimated? Is this estimated from the offline data directly using a standard Bellman error objective? Additionally, the incorporation of average agent observations into the Q-value is not a common practice (to the best of my knowledge) and warrants further explanation.
Lastly, the ground truth $E$ (edge matrix) which is used to train the denoiser is the nearest-neighbor graph. It would help to explain how the final denoising network generated something better than just using the nearest neighbors (as evident in Fig.5, the MCGD-AD baseline).
Theoretical Claims: Theorem 4.1 is sound.
Experimental Designs Or Analyses: I did not find any issues in the experiments following prior Offline MARL approaches and the ablation study on the categorical and anisotropic diffusion. The claims of capturing agent diversity could be better quantified or supported with evidence.
Supplementary Material: I glanced over the proofs and was pleased to see the results on sampling efficiency.
Relation To Broader Scientific Literature: This paper directly addresses the Offline MARL setting like MADIFF (Zhu et al) and methods like OMAR (Pan et al). The idea of capturing agent interactions in multi-agent systems using a graph has been examined previously [3-6] but not via diffusion of the interaction graphs (to the best of my knowledge).
Essential References Not Discussed: References used throughout the review are shown below.
References:
[1] Celebrating Diversity in Shared Multi-Agent Reinforcement Learning, Li et al, NeurIPS 2021
[2] Controlling Behavioral Diversity in Multi-Agent Reinforcement Learning, Bettini et al, ICML 2024
[3] Discrete GCBF Proximal Policy Optimization for Multi-agent Safe Optimal Control, Zhang et al, ICLR 2025
[4] Scaling Safe Multi-Agent Control for Signal Temporal Logic Specifications, Eappen et al, CoRL 2024
[5] Graph Convolutional Reinforcement Learning, Jiang et al, ICLR 2020
[6] Graph Policy Gradients for Large Scale Robot Control, Khan et al, CoRL 2020
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: - The usage of subscripts and superscripts of $t$ is inconsistent (e.g., Pg6 L312 uses a superscript $t$ unlike earlier) and should be fixed.
- Fig. 4 would be better understood if the trajectory states were faded based on time (solid at end of trajectory, faded at beginning).
- If Fig. 1 it would be good to depict the missing ninth agent (there are nine on the left but only eight on the right).
- Some references need to be fixed with the year:
- Shi, D., Tong, Y., Zhou, Z., Xu, K., Wang, Z., and Ye, J. Graph-constrained diffusion for end-to-end path planning
- Trippe, B. L., Yim, J., Tischer, D., Baker, D., Broderick, T., Barzilay, R., and Jaakkola, T. S. Diffusion probabilistic modeling of protein backbones in 3d for the motif-scaffolding problem.
- Vignac, C., Krawczuk, I., Siraudin, A., Wang, B., Cevher, V., and Frossard, P. Digress: Discrete denoising diffusion for graph generation
- For the following, the latest reference is ICLR 2023 :
Wang, Z., Hunt, J. J., and Zhou, M. Diffusion policies as an expressive policy class for offline reinforcement learning
Questions For Authors: 1. What is the intuition behind Eq. 6 and the use of cosine similarity?
2. Could there be added background on the Q-loss used in the anisotropic diffusion loss?
3. What other works consider the incorporation of average neighborhood agent observations into the Q-value loss?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the constructive feedback. We have addressed all comments and revised the manuscript accordingly. Responses are organized by reviewer Weaknesses (W) and Questions (Q), with relevant figures and tables provided in the [anonymized supplementary material](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF).
$\bullet$ W1: Diversity Metrics in Anisotropic Diffusion.
As mutual information-based metrics [1] require costly conditional entropy estimation over agent identity, we adopt System Neural Diversity (SND) [2] to measure action diversity.
On SMAC tasks, we sample $N_1$ observations and generate $N_2$ actions per agent. SND is then estimated using Sinkhorn divergence over pairwise action distances.
As shown in Table 3 (anonymized supplementary), MCGD consistently outperforms MADIFF and DOM2, especially in scenarios with more agents and heterogeneous unit types, validating its effectiveness in modeling diverse coordination.
$\bullet$ W2 and Q1: Intuition behind Transition Matrix.
The matrix $Q$ is based on cosine similarity between agent observations, indicating that agents in similar states are more likely to substitute each other in coordination roles; that is, a higher $Q_{ij}$ implies agent $n_j$ can replace $n_i$.
The formulation of $Q$ follows prior categorical diffusion work [3].
While we use cosine similarity for simplicity, our framework supports alternative metrics, ensuring adaptability across environments.
$\bullet$ W3: Continuous Action Attribute.
In continuous action spaces, the matrix $A_t$ stacks raw actions (dimension $d$) for all agents.
At inference, each agent $n_i$ retrieves the $i$-th row of $\hat{A}_t$ as its action, enabling decentralized execution.
$\bullet$ W4, Q2, and Q3: Q-loss in Anisotropic Diffusion.
Following [4, 5], we add a conservative Q-loss to complement the surrogate loss [6] in offline RL. The full training objective is provided in Equation 1 (anonymous link).
The term $\overline{o}^t_i$ in the Q-value denotes the mean-pooled encoding of neighboring observations, which reduces parameters and enhances generalization when local similarity holds. As shown in the ablation study on observation processing (Table 2, anonymous link), MCGD-AO (average observation) outperforms MCGD-FC (feature concatenation) in both performance and efficiency, validating this design.
$\bullet$ W5: Generated Coordination Graph.
Though trained with nearest-neighbor (NN) graphs as supervision, our graph diffusion model adaptively predicts more informative coordination structures.
As shown in Figure 1 (anonymized supplementary), the denoised graph evolves with agent dynamics—remaining sparse when agents are far apart, and gradually forming structured coordination as they converge. In modified scenarios, the model shifts focus to active agents, deviating from the static NN pattern.
$\bullet$ W6: Capturing Agent Interaction Using Graph Structure.
While prior methods [7–10] have applied interaction graphs in MARL, our work introduces the first graph diffusion-based framework that jointly models structural and action diversity in offline settings.
Building on observation-based heuristics [7], we employ categorical diffusion for edge dynamics and anisotropic diffusion for continuous actions, enabling behavior-adaptive coordination. We plan to explore the integration of advanced graph learning techniques [8–10] in future work.
$\bullet$ W7: Inconsistency between Subscripts and Superscripts.
We have reviewed the manuscript and corrected all inconsistencies.
$\bullet$ W8: Adjusting for Figure 1 and Figure 4.
Figure 4 has been updated with a fading color scheme to better illustrate temporal progression.
In Figure 1, the right subplot depicts a vehicle going offline and remaining stationary, overlapping with its initial position.
$\bullet$ W9: Updated Reference.
We have corrected the references to ensure the years and versions are up-to-date.
References:
[1] Celebrating diversity in shared multi-agent reinforcement learning, Li et al, NeurIPS 2021.
[2] Controlling Behavioral Diversity in Multi-Agent Reinforcement Learning, Bettini at al, ICML 2024.
[3] Graph-Constrained Diffusion for End-to-end Path Planning, Shi et al, ICLR 2024.
[4] Diffusion Policies as an Expressive Policy Class for Offline Reinforcement Learning, Wang et al, ICLR 2023.
[5] Beyond Conservatism: Diffusion Policies in Offline Multi-agent Reinforcement Learning, Li et
al, CoRR 2023.
[6] Dpm-solver: A fast ode solver for diffusion probabilistic model sampling in around 10 steps, Lu et al, NeurIPS 2022.
[7] Graph Convolutional Reinforcement Learning, Jiang et al, ICLR 2020.
[8] Discrete GCBF Proximal Policy Optimization for Multi-agent Safe Optimal Control, Zhang et al, ICLR 2025.
[9] Scaling Safe Multi-Agent Control for Signal Temporal Logic Specifications, Eappen et al, CoRL 2024.
[10] Graph Policy Gradients for Large Scale Robot Control, Khan et al, CoRL 2020. | Summary: This paper introduces MCGD, the first offline MARL algorithm based on graph diffusion models. MCGD employs a discrete diffusion process on graphs to model cooperative relationships among agents, while using a continuous anisotropic diffusion process to model each agent’s action distribution. The authors claim that MCGD can better model the dynamic interactions between agents. The effectiveness of MCGD is validated on multiple offline MARL datasets, with ablation studies conducted for both diffusion processes. Notably, MCGD demonstrates strong robustness, particularly in scenarios where agent attributes and interaction patterns undergo sudden changes.
Claims And Evidence: The claims regarding the effectiveness of the proposed algorithm are well-supported by strong experimental results.
Methods And Evaluation Criteria: The authors validate their approach with commonly used datasets. The proposed graph-based diffusion model is intuitively reasonable, but I have some doubts regarding certain details.
Theoretical Claims: No, I did not check the details of the proof.
Experimental Designs Or Analyses: I have not verified the validity of the experimental results, as the authors have not provided the code, and some details remain unclear to me.
Supplementary Material: I have reviewed the appendix, excluding the proofs.
Relation To Broader Scientific Literature: The proposed algorithm builds upon works in graph diffusion and offline MARL.
Essential References Not Discussed: I have not found any.
Other Strengths And Weaknesses: ### Strengths
1. The experimental results of MCGD are impressive.
2. The algorithm proposed in the paper is novel to me, and the motivation is intuitive.
### Weaknesses
1. Some descriptions in the paper are unclear, making it difficult to understand certain technical details. During sampling, the authors mention using the Q-function to select the optimal action (Line 5 in Algorithm 1). This raises several questions: 1) In a continuous action space, how is the optimal action selected from the Q-function? 2) The Q-function takes as input the average observation of neighboring agents—how is this obtained during testing when other agents’ observations are not directly available? 3) For discrete action spaces, how does the Gaussian diffusion process generate the node action attributes?
2. Additionally, is the node attribute $A_t$ the same as the joint action of the agents? If so, what is the rationale behind defining forward noising in anisotropic noising using the covariance matrix of the agent's action?
3. Some algorithm designs appear rather arbitrary and lack generality. The authors propose using the similarity in the raw observation space as a measure of cooperation between agents. However, observation similarity does not necessarily imply suitability for collaboration, as some tasks may require cooperation between agents with different characteristics. Moreover, such similarity is influenced by the specific meaning of each dimension in the observation space, which varies across different environments. While this property may hold in the environments tested by the authors, it is difficult to claim general applicability. Additionally, using the average observation of neighboring agents as input to the Q-function also lacks generality. Directly averaging observations can lead to significant information loss; for example, if two neighboring agents have values of 0.5 and 0.5 in a certain dimension, their average would be indistinguishable from another pair with values of 0.9 and 0.1, despite the differences in underlying distributions.
Other Comments Or Suggestions: 1. I am particularly interested in how the learned coordination graph structure evolves during task execution. It would be helpful if this could be illustrated in a case study similar to Figure 4.
2. The color saturation in Figure 5 is too high.
Questions For Authors: See weaknesses. If the authors can address my concerns, I am willing to increase my rating.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the constructive feedback. We have addressed all comments and revised the manuscript accordingly. Responses are organized by reviewer Weaknesses (W) and Questions (Q), with relevant figures and tables provided in the [anonymized supplementary material](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF).
$\bullet$ W1.1: Action Selection in Continuous Space.
In the policy sampling phase, each agent $n_i$ generates $N$ random actions from the continuous space to form a candidate set, which is evaluated by the trained Q-function $\mathcal{Q}_{\phi_i}$ to select the action with the highest Q-value.
This replaces the Gaussian noise initialization used in prior methods [1,2], offering a more value-guided and sample-efficient strategy. As selection is over a finite candidate set, the approach naturally applies to both discrete and continuous spaces without requiring action differentiability or closed-form maximization.
$\bullet$ W1.2 and W3.2: Explanation of Average Observation.
To reduce model size and improve scalability, we apply a shared MLP to each neighboring observation and use mean pooling over the extracted features. Compared to concatenation, this approach is more parameter-efficient and robust, particularly as the number of neighbors increases. By focusing on similar neighbors, it also mitigates potential information loss.
Ablation results on SMAC (Table 2 in anonymous link) show that MCGD-AO (average observation) outperforms MCGD-FC (feature concatenation) in both performance and efficiency, validating our design.
During testing, due to decentralized constraints, agents substitute their own observation for the averaged neighbor input, consistent with standard MARL practices.
$\bullet$ W1.3: Gaussian Diffusion over Discrete Actions.
In discrete action spaces, we use one-hot encoding to represent actions and apply softmax decoding at the diffusion model's output. This embeds discrete actions into a continuous latent space for Gaussian diffusion, while allowing valid discrete action reconstruction via softmax followed by argmax during inference.
$\bullet$ W2: Rationale of Covariance Matrix.
The node attribute $A_t$ represents the joint action across all agents in the coordination graph. To enhance coordination modeling, we extend prior works [1–3] by introducing an adaptive covariance matrix in the anisotropic diffusion to capture action uncertainty while preserving the collaboration structure. Inspired by [4], we modify only the covariance (not the mean), avoiding training instability and ensuring convergence and computational efficiency during diffusion.
$\bullet$ W3.1: Observation Similarity for Collaboration.
Our method leverages observation similarity in both initializing the dynamic coordination graph and defining the transition matrix in categorical diffusion.
For initialization, we follow prior work [5] that uses observation similarity to form initial neighbor sets. This provides a flexible starting point, while the diffusion process adaptively refines the graph, enabling coordination even among heterogeneous agents.
In categorical diffusion, cosine similarity between observations defines edge transition probabilities, capturing substitutable coordination. This aligns with adaptive categorical diffusion designs [6]. Other similarity metrics scaled to [0,1] can also be used, ensuring flexibility across environments and observation modalities.
$\bullet$ W4: Learned Coordination Graph.
We illustrate the evolution of the coordination graph in Figure 1 (anonymized supplementary), using the MPE Spread task. The x-axis denotes timesteps, and the y-axis represents different settings.
Initially, the diffusion process disrupts edges due to large agent distances, resulting in independent behavior. As agents converge, the graph recovers a structured form, enabling coordinated behaviors such as landmark assignment.
In modified scenarios, edges shift toward active agents, with Agent 0 either delayed in coordination or excluded entirely. These cases highlight the model’s ability to adapt the graph structure based on real-time agent dynamics.
$\bullet$ W5: Adjusting for Figure 5.
We have reduced the color saturation in Figure 5 to enhance visual clarity.
References:
[1] Beyond Conservatism: Diffusion Policies in Offline Multi-agent Reinforcement Learning, Li et al, CoRR 2023.
[2] Madiff: Offline multi-agent learning with diffusion models, Zhu et al, NeurIPS 2024.
[3] Diffusion-based Episodes Augmentation for Offline Multi-Agent Reinforcement Learning, Oh et al, ICML 2024.
[4] Directional diffusion models for graph representation learning, Yang et al, NeurIPS 2023.
[5] Graph Convolutional Reinforcement Learning, Jiang et al, ICLR 2020.
[6] Graph-Constrained Diffusion for End-to-end Path Planning, Shi et al, ICLR 2024.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors' clarification of my questions, as well as the additional experiments and visualizations. The proposed algorithm is relatively complex, with many details requiring clearer explanation for the reader to fully understand. I recommend that the authors substantially revise the methodology section to include more detailed descriptions where necessary. Considering the strong empirical performance and the results of the additional experiments, I am changing my rating to weak accept. | Summary: This paper uses a graph diffusion approach to study MARL problems. This method incorporates graph diffusion in order to incorporate changes in multi-agent coordination dynamics (such as an agent dropping out). The goal of the approach is to be able to more seamlessly handle out-of-distribution states and actions than alternative MARL approaches. Experimental results indicate that the method performs well empirically.
Claims And Evidence: Yes, it seems that the authors have presented experimental results that support the claims with empirical evidence.
Methods And Evaluation Criteria: I am not an expert in applied MARL research, so I am not sure what is standard, but the examples seemed logic and reasonable to me.
Theoretical Claims: I skimmed the proof and it seemed reasonable.
Experimental Designs Or Analyses: It seems that most of the MARL settings considered have relatively few number of agents (I believe less than 10 agents, is that correct)? I'm curious how well the method scales to more agents, especially given the computational costs of diffusion models in general.
Supplementary Material: I skimmed the proof.
Relation To Broader Scientific Literature: I am unsure of the state of the art as I am not an expert in this domain.
Essential References Not Discussed: I am unsure of whether references are complete, but it seems the authors made a solid effort.
Other Strengths And Weaknesses: The paper is overall well written and it seems the authors have made an effort to provide a detailed explanation of the forward and backward denoising process.
Other Comments Or Suggestions: Please see questions below.
Questions For Authors: (1) How well can the method scale and how expensive is it compared to the other baselines?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the constructive feedback. We have addressed all comments and revised the manuscript accordingly. Responses are organized by reviewer Weaknesses (W) and Questions (Q), with relevant figures and tables provided in the [anonymized supplementary material](https://anonymous.4open.science/r/MCGD_Rebuttul-23DF).
$\bullet$ W1 and Q1: Scalability Comparison.
To ensure fair and comparable evaluation, we adopt similar experimental settings to prior diffusion-based offline MARL works [1-3], where most tasks involve fewer than 10 agents. However, this does not suggest our method is limited to small-scale scenarios.
As detailed in Appendix 7.4.2, we compare the policy sampling time of our method with MADIFF, showing that despite the additional cost from structural diffusion, our approach remains computationally competitive.
To assess scalability and collaborative performance in larger-scale settings, we further conduct experiments on the MPE Spread task with 8, 16, 32, and 64 agents. As presented in Table 1 of the anonymized supplementary material, MCGD consistently outperforms MADIFF and DOM2 across all scales, with performance gains increasing as the number of agents grows. These results demonstrate that our graph diffusion-based design not only scales well but is also more effective in modeling complex multi-agent coordination.
References:
[1] Beyond Conservatism: Diffusion Policies in Offline Multi-agent Reinforcement Learning, Li et al, CoRR 2023.
[2] Madiff: Offline multi-agent learning with diffusion models, Zhu et al, NeurIPS 2024.
[3] Diffusion-based Episodes Augmentation for Offline Multi-Agent Reinforcement Learning, Oh et al, ICML 2024. | null | null | null | null | null | null |
Hot PATE: Private Aggregation of Distributions for Diverse Tasks | Reject | Summary: Hot PATE extends the Private Aggregation of Teacher Ensembles (PATE) framework to diverse and open-ended tasks, addressing the fundamental tradeoff between privacy and diversity in generative AI. While the PATE framework works best in the classification settings with a small set of labels, Hot PATE can remedy this with coordinated ensembles, where teacher models use shared randomness to synchronize token selection, increasing agreement while preserving diversity without additional privacy penalties. The authors formalize a diversity-preserving aggregation method that ensures knowledge transfer while filtering irrelevant tokens. The benefits of coordinated ensembles are demonstrated t oachieve high diversity in an artificial scenario designed by the authors empirically.
## update after rebuttal
The reviewer thanks the authors for their responses. While I appreciate the effort to clarify the points raised, I feel that the answers do not fully resolve my concern about the empirical section, and as such, I am maintaining my original score.
Claims And Evidence: While the submission presents strong theoretical foundations regarding the privacy-diversity tradeoff in PATE and the benefits of coordinated ensembles, the empirical evaluation is pretty weak and does not provide convincing evidence.
Methods And Evaluation Criteria: The proposed methods are really great and intuitive for the problem or application at hand but the evaluation is quite weak. It relies on an artificial setting that does not fully reflect real-world applications.
Theoretical Claims: I have not fully verified the proofs.
Experimental Designs Or Analyses: The experimental design is highly artificial and does not map directly to practical use cases, which limits the generalizability of the findings. The empirical results do not include concrete privacy budget values (epsilon, delta), which are crucial for evaluating privacy-preserving methods. There is also not sufficient ablation studies that systematically study how the parameters affect results.
Supplementary Material: I went over the Appendix of the paper.
Relation To Broader Scientific Literature: The paper improves a key limitation of PATE over generative tasks where outputs are inherently diverse, offering an important advancement by improving diversity preservation in private learning. This can be beneficial in scenarios such as in-context learning and synthetic text generation for distillation.
Essential References Not Discussed: I think the paper presents the background material adequately.
Other Strengths And Weaknesses: Strengths:
- The paper presents a creative extension of PATE to diverse and open-ended tasks, which is a significant departure from prior applications primarily focused on classification.
- The introduction of ensemble coordination to enhance diversity in a privacy-preserving manner is a novel approach in privacy-preserving learning.
- The paper provides a rigorous mathematical framework for diversity-preserving aggregation.
Weaknesses:
- The evaluation is limited to a synthetic task rather than real-world applications.
- The empirical section does not report exact (epsilon, delta) values for different settings and it does not explicitly measure how privacy budgets scale with diversity.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Similar to the prior work, it'd be very helpful to try Hot PATE on real-world datasets to substantiate the practical impact of Hot PATE and improve confidence in its general applicability.
2. Along with the point above, can you provide some results on different privacy levels to better understand empirically the diversity-privacy trade-off.
The reviewer is not concerned about the contribution of the approach introduced in the paper, however, the empirical section is pretty weak. It'd definitely make the paper stronger if the authors provide empirical studies on real-world datasets and various privacy levels.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the time and comments.
**Question 1**
*״Try Hot PATE on real-world datasets to substantiate the practical impact of Hot PATE and improve confidence in its general applicability״*
Hot PATE is a mathematically rigorous framework, which we consider to be our main contribution. Hot PATE **can only improve** over the baseline (cold PATE) in terms of privacy utility tradeoff, and this benefit increases with the diversity.
We include here additional evidence of large potential gains of hot vs cold PATE on **natural texts** that represent real-world datasets. We are happy to add such evaluations to the paper:
We generated the tokens output distributions of Llama 3.2 1B on all prefixes of the first 500 tokens of a WSJ top page article from Saturday (this is representative, as other news articles and texts we tried gave similar results). The temperature setting was the default $T=1$.
For the purpose of this evaluation, consider a case when all $n$ teachers share the same output distribution. In this case, a coordinated ensemble would yield a histogram where a single token (different one for different shared randomness) has a count of $n$ and remaining tokens have count $0$. The diversity-preservation is perfect as the probability of any one token is equal to its probability value in the distribution. As for cold PATE, we computed the agreement level (minimum fraction of teachers) required for meeting different diversity-preservation levels on a sequence of 10 tokens. These values are inversely related to the privacy parameter $\varepsilon$. Results are averaged over a sliding window of 10 consecutive tokens from the article:
Hot PATE (coordinated ensembles):
100% diversity transfer, privacy parameter $\varepsilon$.
Cold PATE (independent ensembles):
| Diversity Transfer | Count Required | × Loss in $\varepsilon$ |
|--------------------|--------------------|--------------------------|
| 25% | 0.084 *n* | 11.9 |
| 50% | 0.0261 *n* | 38 |
| 90% | 0.000733 *n* | 1364 |
| 95% | 0.000184 *n* | 5446 |
As you can see, for transferring 50% of the distribution, we would incur X$38$ privacy loss with cold PATE. For transferring 95%, the loss is X$5446$. This is very significant. We can extrapolate the same relative gains when the teacher distributions are not identical, as the gains would apply to a common "transferable" part that is supported by enough teachers.
**Question 2**
״Can you provide some results on different privacy levels to better understand empirically the diversity-privacy trade-off.״
Yes. There are two regimes:
(1) The teacher distributions are "close" in TV distance. In this regime, using Hot PATE allows us to generate the privacy-preserving tokens (called "yields") for "free". We achieve this using the SVT (sparse-vector technique) with "BetweenThresholds" as there is a high agreement among the teachers. In contrast, in this regime, the baseline "cold" PATE incurs a privacy cost that increases with the diversity, and does not obtain "free yields" as our method.
(2) The teacher distributions are less similar (higher TV distance). In this regime it could be that when sampling a token from each teacher, the resulting samples are in complete "disagreement" and we need to re-sample (so multiple samplings might be needed per generated token). What we showed is that in Hot PATE we essentially need to pay only once per "yield", and we can generate tokens as long as most teachers agree on some small fraction of the distribution (in TV distance). In contrast, in this regime, the baseline "cold" PATE fails completely, in the sense that the probability of it generating any tokens at all is close to zero.
We did include some calculations in the appendix using one particular Laplace-based analysis method. For $\varepsilon=1$, we get $0.005/(2 ln(1/\delta)) * n^2$ tokens for $\delta=10^{-6}$. So this is 180 tokens with 1000 "teachers" (partitions of the data), 18000 tokens with 10K teachers, or 7 tokens for 200 teachers. These tokens are the combined length of synthetic examples or summaries generated from the sensitive data.
Finally, if more utility is needed, then hot PATE also applies with weaker privacy notions that are often used in practice, such as DP with high $\varepsilon$ or $k$-anonymity (as used in Clio by Anthropic): The "boost" in the privacy parameter facilitated by high counts in the histogram translate to a "boost" in $k$. | Summary: The PATE framework was designed for classification tasks where there is a single ground-truth label; however for tasks like sequential text generation, there might be multiple “good” responses. This paper proposes to extend the PATE framework to diverse tasks like this (where the responses are distributions rather than a single outcome) by designing an aggregation method that preserves both diversity and privacy.
## update after rebuttal:
After reading the other reviews and the rebuttals, I do have an amendment to make: I wrote down “Convincing empirical evaluation” as a strength, but the empirical evaluation is only convincing with regards to demonstrating that hot PATE preserves diversity. The experiments don’t fully demonstrate the value of diversity with regards to practical real-world use-cases.
Still (and somewhat subjectively), I think this paper has strong merits just in terms of theoretical foundations and sheer creativity; it is a significant departure from previous work and I think would be interesting to audiences at ICML, despite its limitations.
Claims And Evidence: The claims made in the submission are supported by evidence.
Methods And Evaluation Criteria: The proposed methods make sense for the problem at hand.
Theoretical Claims: I didn't thoroughly check the correctness of any proofs.
Experimental Designs Or Analyses: The empirical demonstration in Section 5 looks sound to me.
Supplementary Material: I didn't review the supplementary material carefully.
Relation To Broader Scientific Literature: This paper's key contribution is an extension of the PATE framework.
Essential References Not Discussed: All essential references are discussed.
Other Strengths And Weaknesses: Strengths --
- The paper's ideas are novel and it is great to see PATE applied in a more modern setting.
- Convincing empirical evaluation.
- Figures 1-3, in addition to being very charming, are helpful tools for understanding the text.
Weaknesses --
- The paper is pretty dense and it is easy to lose the plot.
- To some extent, the paper feels like a "proof of concept" to me: we get a new framework and we see that it does well according to certain metrics, but it's unclear how well this will perform across different applications because there is no utility guarantee and no downstream task.
Other Comments Or Suggestions: This paper has great ideas but is nuanced and requires careful reading. I have a couple thoughts on how to make things more palatable for a casual reader:
- I think it would be great to have a more explicit side-by-side comparison of cold PATE and hot PATE. One way to do this could be to have a “master” algorithm block that generalizes both cold and hot PATE. Then cold PATE could be characterized as plugging in DP-aggregation of the frequency histogram into this master algorithm block, and hot PATE could be characterized as plugging in a diversity-preserving aggregation method (as detailed in Definition 1).
- Section 4 could also better juxtapose independent ensembles (for cold PATE) and coordinated ensembles (for hot PATE). I do like the blue comments in Algorithm 1 but in the two-column format (with the comments overflowing onto the next line and hampering readability) I think it hinders as much as it helps. A “master algorithm block” type of solution could also work here, to highlight the differences between the two sampling methods. (And if I’ve understood correctly, the main difference between independent and coordinated ensembles is mostly just how $y_i$ is sampled, and the $c_j$ are computed the same way for both methods.)
- Lastly I really liked the explanation of “cold” vs “hot” PATE that appears in Section 2, and I feel like it could be moved to the introduction to avoid suspense. (I spent the first four pages of the paper a little distracted, wondering what makes PATE “hot” or “cold”.)
Questions For Authors: Besides sequential text generation, what other applications would hot PATE work well for?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the constructive feedback and excellent comments and suggestions. We will use them to improve the presentation.
**Question:** *“Besides sequential text generation, what other applications would hot PATE work well for?”*
**Response:**
Hot PATE is suitable for "soft" tasks where the desired output is a sample from a distribution over multiple "possible answers" or "responses". It is a way to aggregate multiple sensitive distributions in order to obtain one or multiple samples that preserve "diversity" and "privacy" (this could also be a single task; not necessarily sequential generation).
Example usage that is not LLM token generation: A game where each sensitive expert suggests a distribution over possible next moves. We want to choose a move that reflects the experts but guards their privacy.
Hot PATE is also suitable for a weaker notion of privacy, a variant of $k$ anonymity, when we only require that the output is “supported” by at least $k$ sensitive units. To achieve this, we simply only return a response that has count at least $k$ without adding noise. With hot PATE there is a much higher likelihood of a token having a large count than with cold PATE.
**Weaknesses:**
The reviewer pointed out that it is hard to tell how hot PATE would *“perform across different applications” and “utility guarantee”.*
Since indeed our demonstration was on a particular task, we include here some additional evidence of large potential gains of hot vs cold PATE on natural texts. We are happy to add such evaluations to the paper. We also discuss utility guarantees (see our response to reviewer GoNr).
We considered the token output distributions of Llama 3.2 1B on all prefixes of the first 500 tokens of a WSJ top page article from Saturday (other texts gave similar results). The temperature setting was the default $T=1$.
For the purpose of this evaluation, consider a case when all $n$ teachers share the same output distribution. In this case, a coordinated ensemble would yield a histogram where a single token (different one for different shared randomness) would yield a count of $n$. The diversity-preservation is perfect as the probability of any one token is equal to its probability value in the distribution. As for cold PATE, we computed the agreement level (minimum histogram count) required for meeting different diversity-preservation levels on a sequence of 10 tokens. These values are inversely related to the privacy parameter $\varepsilon$. Results are averaged over a sliding window of 10 consecutive tokens from the article:
Hot PATE (coordinated ensembles):
100% diversity transfer, privacy parameter $\varepsilon$.
Cold PATE (independent ensembles):
| Diversity Transfer | Count Required | × Loss in $\varepsilon$ |
|--------------------|--------------------|--------------------------|
| 25% | 0.084 *n* | 11.9 |
| 50% | 0.0261 *n* | 38 |
| 90% | 0.000733 *n* | 1364 |
| 95% | 0.000184 *n* | 5446 |
As you can see, for transferring 50% of the diversity, we would incur X$38$ privacy loss with cold PATE. For transferring 95%, the loss is X$5446$. This is very significant. We can extrapolate the same relative gains when the teacher distributions are not identical, as the gains would apply to a common "transferable" part that is supported by enough teachers. | Summary: This paper introduces Hot PATE, a privacy-preserving method for auto-regressive models in open-ended tasks. It addresses the challenge of preserving diversity and privacy by coordinating teacher models through shared randomness and positive correlation voting. Key contributions include mathematically formalizing robust diversity transfer and demonstrating significant improvements over traditional methods, particularly in maintaining higher coverage and diversity with lower noise scales. Applications range from homogeneous to heterogeneous ensembles, enabling flexible privacy-preserving multi-party learning.
## update after rebuttal
I maintain my score after carefulling reading the rebuttal.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I've not checked the proofs in appendix
Experimental Designs Or Analyses: The paper focuses more on theoretical advantages and does not thoroughly explore the feasibility, computational costs, and scalability of the coordination integration method in real-world scenarios. These factors are critical for practical deployment.
Supplementary Material: I've not review the supplementary material
Relation To Broader Scientific Literature: This paper have close relation to PATE and differential privacy.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Weakness:
1. Redundant Contribution Section:
The contribution section is overly verbose and repetitive, covering multiple details and steps repeatedly. For instance, the paper repeatedly elaborates on the implementation mechanisms of "Hot PATE" (such as specific sampling methods for coordination sets, threshold settings, etc.) and emphasizes the same core ideas across different scenarios (homogeneous and heterogeneous sets).This redundancy makes the contribution section overly cumbersome and less focused.
2. Lack of Clear Hierarchical Structure:
The contribution section fails to distinguish between core innovations and secondary implementation details. For example, the proposal of "coordination sets" is one of the main contributions of the paper, but it is mixed with other technical details (e.g., privacy analysis methods), making it difficult for readers to quickly grasp the key points.
Other Comments Or Suggestions: No
Questions For Authors: 1. The experimental section only counted the diversity of tokens, does the dataset composed of these tokens have practical application value? (For example, are the generated sentences still grammatically correct? Can you provide a case of the generation results?)
2. Is the diversity-privacy tradeoff indeed inherent? What's your final answer for this question.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for the comments and will do our best to improve the presentation.
**Question 1:**
-- *our demo “only counted the diversity”*.
Our demo reports on the diversity-privacy tradeoff. Diversity is measured by the number of returnable tokens for a **given privacy level** (measured by the threshold setting).
-- *“grammatically correct”*
Our proposed method returns text that is generated by the LLM. So if the LLM generates grammatically correct sentences, then so does our output. This is true in our construction because all of the teachers are consistently applied with the same sanitized prefix (which was privately computed in the previous iterations). So all of the teachers are predicting the next token of the same prefix. This is explained on page 4 (below Figure 4). In our demo, we used the Lamma 3 8B model and text prompts. The prompts were designed to generate a single token response that is a number and the LLM behaved as expected. Sequential text generation repeats such steps.
-- “practical application value”.
Our hot PATE method is designed as a plug-in replacement for cold PATE. It is validated mathematically, always improves the utility-privacy tradeoff, and its benefits increase with the entropy of the generation process.
We include here an **additional evidence** for the benefits of hot PATE over baseline cold PATE on **natural texts**. We considered the token output distributions of Llama 3.2 1B on all prefixes of the first 500 tokens of a WSJ top page article from Saturday (other texts gave similar results). We are happy to include such evaluation in our paper.
For the purpose of this evaluation, consider a case when all $n$ teachers share the same output distribution. In this case, a coordinated ensemble would yield a histogram where a single token (different one for different shared randomness) would yield a count of $n$. The diversity-preservation is perfect as the probability of any one token is equal to its probability value in the distribution. As for cold PATE, we computed the agreement level (minimum histogram count) required for meeting different diversity-preservation levels on a sequence of 10 tokens. These values are inversely related to the privacy parameter $\varepsilon$. Results are averaged over a sliding window of 10 consecutive tokens from the article:
Hot PATE (coordinated ensembles):
100% diversity transfer, privacy parameter $\varepsilon$.
Cold PATE (independent ensembles):
| Diversity Transfer | Count Required | × Loss in $\varepsilon$ |
|--------------------|--------------------|--------------------------|
| 25% | 0.084 *n* | 11.9 |
| 50% | 0.0261 *n* | 38 |
| 90% | 0.000733 *n* | 1364 |
| 95% | 0.000184 *n* | 5446 |
As you can see, for transferring 50% of the diversity, we incur X$38$ privacy loss with cold PATE. For transferring 95%, the loss is X$5446$. This is very significant. We can extrapolate the same relative gains when the teacher distributions are not identical, as it applies to the "transferable" part.
**Question 2:**
As we establish mathematically, and demonstrate in our demo, hot PATE (coordinated ensembles) provides high utility regardless of diversity. The tradeoff is not inherent.
**Weaknesses:**
– *"focuses more on theoretical advantages and does not thoroughly explore the feasibility, computational costs, and scalability of the coordination integration method in real-world scenarios"*
The benefits of our method are established via a *rigorous mathematical analysis* and kick-in whenever there is entropy in the responses (which is well established for LLMs). We do, in fact, include a discussion of scalability and computational costs for different API types (Section 4.3). The additional evidence provided above shows that on "real-world" text generation we can expect orders of magnitude benefits over "cold" PATE.
– *“repeat the same core idea across scenarios” by describing “homogeneous and heterogeneous” ensembles*
These two scenarios warrant separate treatment. Standard PATE is designed for heterogeneous ensembles, which make sense both in diverse and non-diverse settings, whereas homogeneous ensembles are only relevant in diverse settings (and as far as we know were not previously studied with PATE). They require not only different threshold settings but also different private aggregation methods, in order to preserve diversity.
– *״The proposal of "coordination sets" is one of the main contributions of the paper, but it is mixed with other technical details (e.g., privacy analysis methods)״*
Our submission is about privacy. It is therefore necessary and central for us to present coordinated ensembles together with their benefit to our privacy analysis. | null | null | null | null | null | null | null | null |
Online Uniform Sampling: Randomized Learning-Augmented Approximation Algorithms with Application to Digital Health | Reject | Summary: The authors propose an algorithm for online uniform sampling (OUS) to distribute a constrained sampling budget across unknown decision times as uniformly as possible over risk times. They consider cases of whether the number of risk times is both known and unknown, and present algorithms for both scenarios that are supported by both theoretical and empirical results.
Claims And Evidence: To the best of my knowledge, I believe the claims made in the submission are supported by clear and convincing evidence. The authors cite relevant work, derive reasonable theoretical results, and present empirical findings that support the claims made in the paper. Regarding the claim in lines 208-211, left column, I am unable to validate this claim and defer to more knowledgeable reviewers.
Methods And Evaluation Criteria: Both the synthetic and mHealth datasets make sense for the problem at hand. Given the lack of baselines in the OUS research field as stated by the authors, the authors could potentially run their method on additional relevant dataset(s) and tasks (e.g., some options are listed [here](https://depressioncenter.org/research-services/mobile-technologies-core/mobile-health-datasets)) to better demonstrate the empirical efficacy of their method, although I would still recommend acceptance of this work as is without such additional experiments.
Theoretical Claims: I checked for the correctness of the Proofs in Appendix C, and have the following follow-up question:
1. In the equations presented on pages 11 and 12 regarding the proofs for Subroutines 1 and 2, the authors make the following approximations:
$$f(b):=b-\frac{b}{e-1}\log(e-1)+\frac{b}{e}\approx b$$
$$g(b):=\frac{2b}{e}+\frac{b}{e-1}-\frac{2b}{e^2} \approx b$$
where I define $f(b), g(b)$ for convenience of discussion. It seems that both $f(b), g(b) > b$ for all $b > 0$. Wouldn't this mean that the bound on the expectation budget may not be upper-bounded by $b$ even if it is upper bounded by $f(b), g(b)$?
Experimental Designs Or Analyses: I have checked for the soundness of the experimental design and analysis of both the synthetic and real-world experiments presented, and believe that they are sound to the best of my knowledge.
Supplementary Material: I have reviewed Appendices A-F, and the code included in the supplementary material - both of which appear reasonable to the best of my knowledge.
Relation To Broader Scientific Literature: The idea of OUS as a field is interesting to me, and I agree with the authors that prior work in this field is sparse given my (frankly limited) experience in the digital health-ML literature. While the algorithms introduced by the authors are notable, I think one of the key contributions of this work is the authors' principled formulation of OUS as an online optimization problem, and defining relevant metrics and definitions to characterize algorithms in this space.
Essential References Not Discussed: The references included by the authors are extensive and seem reasonable to me. I do not currently do research in this space and am not well-versed enough with existing literature in this research area to comment on if any references are missing.
Other Strengths And Weaknesses: ## Strengths
2. In general, this is a well-written manuscript with notable clarity and presentation - I do not personally do research in this field, yet was able to follow the contributions and mathematical formulation of this paper quite easily even on the first pass.
## Weaknesses
In general, the "weaknesses" listed below are more so clarifying questions for myself.
3. Is the assumption for binary risk levels (line 85, right column) commonly used in the literature? How might the framework proposed in this paper extend to the continuous risk setting, which could offer a more descriptive picture of patient state? I appreciate the discussion of the extension to multiple risk levels by the authors in Appendix A, although would like to see empirical results to support the practical tractability of this extension to approximate a pseudo-continuous risk setting (e.g., including experimental results on the Heartsteps task by defining different risk levels through binning by number of steps in the prior 40 minutes).
4. What does “arbitrarily” mean in the context of line 89, right column? Does it truly mean the risk distribution is treated as random as a function of time, or can the problem formulation be treated as an MDP with treatments (or lack thereof) as the action space?
5. Is the $\rho$-robustness guarantee in lines 199-202 achievable in practice for non-trivial values of $\rho$? I would imagine that achieving such a bound for arbitrarily inaccurate estimates for $\tau^*$ is challenging if not impossible.
6. In line 371, right column, is there a clinical motivation for the choice of 150 steps to define the risk variable? Perhaps a relevant citation(s) or additional discussion would help support this choice.
Other Comments Or Suggestions: - [Line 332, right column] “inAlgorithm 2” is missing a space.
- Should the x-axis correspond to user-days instead of “Width” in Figure 3?
Questions For Authors: Please see my main numbered comments in the **Theoretical Claims** and **Other Strengths and Weaknesses** sections above. If the authors are able to address my numbered comments [1], [3], and [5] above, I would be happy to increase my score recommendation. Comments [4] and [6] are helpful for potential discussion (whether only in the discussion period or in the final manuscript as well), but would likely not change my evaluation of the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are glad that the reviewer found our paper "well-written with notable clarity and presentation." We thank the reviewer for the valuable feedback and respond them in detail below.
- **Proof of Lemmas 3.1 and 4.1** Sorry for the sloppiness in the proofs. To ensure exact satisfaction of $\mathbb{E}\left[\sum_{i=1}^{\tau^*} p_{i}\right] \leq b$, one can appropriately scale the input budget $b$ in Algorithms 1 and 2. For example, for Subroutine 2, the input budget should be set as $b/1.047$. In our experiments, we have implemented this adjustment to guarantee that the budget constraint is strictly satisfied. We will revise the statement of the lemmas and theorems to reflect this.
- **Multiple risk levels** Binary or categorical risk levels are common in digital health studies. For instance, the HeartSteps study defines risk levels as binary, with fewer than 150 steps in the previous 40 minutes considered "at risk", and otherwise "not at risk". Similarly, in the Sense2Stop Smoking Cessation Study [2], the risk variable takes on three categories: stress, no stress, and unknown. Each distinct risk category typically requires a separate budget input, resulting in independent subproblems.
In a truly continuous risk setting, the probability of observing any specific risk value is effectively zero, making the OUS formulation unsuitable. However, a pseudo-continuous setting is feasible by discretizing risk into different levels and applying our proposed methods separately for each category, as described in Appendix A. We provide empirical results demonstrating this approach using the HeartSteps data, categorizing step counts into three levels: fewer than 50, fewer than 100, and fewer than 150 steps. The results suggested that our proposed learning-augmented algorithm in general has the best performance. Figures illustrating these results are available at the following link: https://imgur.com/a/UXRotSQ
- **l89, arbitrarily** By "arbitrarily," we mean that the distribution of risk levels can change adversarially over time without assuming an underlying structure like an MDP. Since interventions may unpredictably influence future risks, our algorithm is designed to ensure strong performance guarantees even in the worst case. We will clarify this in l89.
- **$\rho$-robustness** Thank you for the question. Lines 119–122 explicitly state the conditions for achieving $\rho$-robustness. In maximization problems like OUS, the goal is to design an approximation algorithm with the highest possible robustness factor $\rho$. Theorems 3.2 and 4.2 specify the robustness factors that our algorithm can achieve, demonstrating satisfactory performance. Non-trivial robustness levels, such as $\rho > 1-\frac{1}{e}$ are typically challenging or impossible to achieve for maximization problems, as supported by existing literature [3].
- **clinical motivation for risk variable** Thank you for raising this. Yes, previous clinical studies define sedentary behavior as inactivity having at least 40 minutes of time with fewer than 150 steps. We will include additional reference [1] to reflect this.
- **x-axis of Figure 3** Thank you for the question. The x-axis correctly represents "Width," not user-days, as the average competitive ratio shown is computed across user-days for varying widths of the prediction interval. We display results across different confidence interval widths to assess algorithm performance under predictions ranging from extremely good to extremely bad, thereby testing their robustness in practice.
Thank you for catching the typo. We have corrected it.
- [1] Spruijt-Metz, et al. (2022). Advancing behavioral intervention and theory development for mobile health: the HeartSteps II protocol. International journal of environmental research and public health.
- [2] Battalio, S. L., et al. (2021). Sense2Stop: a micro-randomized trial using wearable sensors to optimize a just-in-time-adaptive stress management intervention for smoking relapse prevention. Contemporary Clinical Trials.
- [3] Buchbinder, N., et al. (2007). Online primal-dual algorithms for maximizing ad-auctions revenue. In European Symposium on Algorithms.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their thoughtful rebuttal and hard work. All of my initial concerns raised in my initial review have been addressed/will be addressed in the camera-ready version, and I will increase my score to 4. However, I do note that I do not regularly do research in this space and acknowledge that my review may have missed more niche/domain-specific points - for this, I defer to the expertise of more knowledgeable reviewers. | Summary: This paper studies the following online prediction problem: Let $\tau^*$ be an unknown number in $[b,T]$, where $b$ and $T$ are known. At every step $t\le \tau^*$, the learner needs to predict a number $p_t\in [0,1]$. The goal is to maximize
$
\sum_{t=1}^{\tau^*}p_t-\frac{1}{\tau^*}\ln\left(\frac{\max_t p_t}{\min_t p_t}\right)
$
subject to the constraint
$
\mathbb{E}\Big[\sum_{t=1}^{\tau^*}p_t\Big]\le b,
$
where $\mathbb{E}$ denotes the expectation with respect to the internal randomness of the prediction algorithm.
The paper provides an algorithm that achieves a constant competitive ratio for the above objective compared to the optimal offline solution (where $\tau^*$ is known). The paper further provides an argument demonstrating that the competitive ratio cannot be better than $0.504$. Finally, the paper considers the case when $\tau^*$ can be predicted within a certain interval and demostrate the ultility of the approach in the context digital health.
Claims And Evidence: First of all, the problem formulation seems quite problematic since the term
$
\frac{1}{\tau^*}\ln\left(\frac{\max_t p_t}{\min_t p_t}\right)
$
can be negligible even if $p_t$ decreases polynomially with respect to $t$. One can simply assign $p_t$ to be any convergent series, such as
$
p_t \propto \frac{1}{t^2}.
$
In this case, the competitive ratio can easily be made to approach $1$, provided that $\tau^* \gg b$. This suggests that the proposed problem might be essentially trivial.
The authors also claim that no algorithm can achieve a competitive ratio better than $0.504$. However, I find the proof problematic. Specifically, how can one assume that the optimal strategy must be decreasing? While I understand that this should be the case for the "sum part" via the rearrangement inequality, what about the "log penalty" part?
Methods And Evaluation Criteria: As far as I understand, the proposed method is essentially a "doubling trick", which is widely used in the online learning literature to obtain time-independent guarantees, with some tweaks to the specific parameter regime.
Theoretical Claims: I verified some of the proofs, such as Lemma 3.1 and Theorem 3.2, and they appear to be correct (i.e., I did not identify any significant technical issues).
Experimental Designs Or Analyses: The paper conducts some evaluations using synthetic and real data, which look reasonable to me. However, since I am not familiar with the compared benchmarks, I cannot comment on the significance of the experimental results.
Supplementary Material: I did not review the supplementary material, as the paper is primarily theoretical.
Relation To Broader Scientific Literature: As far as I understand, the primary contribution appears to be providing a mathematical formulation for a particular application scenario in digital health.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: **Other Weaknesses:**
1. The problem studied is more of an algorithmic design problem rather than a learning problem. From a machine learning perspective, the problem introduced is quite trivial, as the environment provides nearly no feedback (except for termination). Therefore, I believe the paper might not quite fit within the scope of ICML.
2. The paper provides no intuition behind the design of the algorithms. For example, why choose the distribution proportional to $1/\alpha$, and why choose the constant $e$? My impression is that the selection of such parameters appears quite arbitrary, and the authors did not put enough effort into optimizing and justifying these choices.
Other Comments Or Suggestions: The $\sigma$ that first appears on page 3 (line 139, right) is not defined.
Questions For Authors: Please answer the questions in **"Claims and Evidence"** and address the concerns in **"Other Strengths and Weaknesses."**
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's feedback. We clarify that our work is positioned as an applied paper motivated by digital health applications rather than a purely theoretical paper. Below, we illustrate the type of guarantees that competitive ratios provide, detail the computation of competitive ratios, and explain how this work aligns with the ML community.
- **is penalty term negligible** Consider your example where the series converges as $p_i \propto \frac{1}{i^2}$. Suppose $b=2$ and $\tau^*=4$. The resulting treatment probability sequence is $1$, $\frac{1}{4}$, $\frac{1}{9}$, $\frac{1}{16}$. Then, the penalty term becomes $\frac{1}{4}\ln \frac{1}{1/16} = \frac{\ln 16}{4}$. The objective function becomes $1+\frac{1}{4}+\frac{1}{9}+\frac{1}{16}-\frac{\ln 16}{4} \approx 0.73$. This yields a competitive ratio of approximately $\frac{0.73}{2} \approx 0.365$. Although as $\tau^*$ grows large, the penalty term $\frac{1}{\tau^*}\ln \frac{1}{1/{\tau^*}^2} = \frac{2\ln \tau^*}{\tau^*}$ becomes negligible, this does not imply that the competitive ratio approaches 1 in general.
Since our problem makes *no* assumption on the distribution of $\tau^*$ and the competitive ratio must hold for the worst-case instance, the challenge arises precisely when $\tau^*$ is close to the budget $b$. Thus, the problem remains non-trivial.
- **upper bound derivation** In our proof, we do not require the policy to be non increasing. Sorry for the typo, we have corrected it as below. To derive the upper bound of 0.504 using Yao's lemma, we constructed a challenging instance and solved the following maximization problem over probabilities $p_1, \dots, p_5 $:
\begin{align*}
\arg \max_{p_1, p_2, p_3, p_4, p_5}\pi_1p_1 + \pi_2(p_1+p_2) + \pi_3(p_1+p_2+p_3) + \pi_4(p_1+p_2+p_3+p_4) + \pi_5 b - \pi_2\frac{1}{2} \left|\ln\frac{p_1}{p_2}\right|-\pi_3\frac{1}{3}\left|\ln\frac{p_1}{p_3}\right| - \pi_4\frac{1}{4}\left|\ln\frac{p_1}{p_4}\right| - \pi_5\frac{1}{5}\left|\ln\frac{p_1}{p_5}\right|
\end{align*}
subject to $p_1+p_2+p_3+p_4+p_5=b$.
We mistakenly omitted the absolute value in the current proof. Notably, despite no explicit constraint enforcing a decreasing solution, the optimal solution naturally followed this pattern, suggesting that decreasing or non-increasing probabilities generally improve performance in the OUS problem.
- **Doubling trick** In our problem formulation, there is no reward learning, so neither our method's inspiration nor our analysis techniques stem from online learning problems. While our algorithm design may resemble the doubling trick used in learning, the analysis objectives and problem complexities are fundamentally different.
- **scope of ICML** We acknowledge that this paper focuses on online optimization, specifically the design of randomized approximation and learning-augmented algorithms, rather than traditional online learning. Online optimization, especially with prediction augmentation, is actively studied in machine learning. Related works, such as [1] (ICML 2023) and [2] (NeurIPS 2020), demonstrate its relevance in top-tier conferences. Thus, we believe our paper aligns well with ICML's scope.
- **parameter choices in algorithm design**
We chose the distribution $\propto 1/\alpha$ and the constant $e$ for a cleaner analysis of the algorithm’s expected performance, particularly for integration. The choice of $e$ aligns with classical online maximization results where optimal competitive ratios often take the form $1 - 1/e$ [3]. It is further inspired by the randomized algorithm of [1].
We have clarified this in the revised version (l208):
>We choose the density $1/\alpha$ and the constant $e$ to simplify the analysis of the algorithm’s expected performance. The choice of $e$ is also motivated by its frequent appearance in upper bounds for online optimization problems.
- **l139, $\sigma$:** The tunable parameter $\sigma$ is introduced on l139 (right column), allowing us to explore a range of values that penalize non-uniformity at different scales. We have now revised l139:
> The tunable parameter $\sigma$ in the penalty term $\sigma \cdot \ln \frac{\max_i p_i}{\min_i p_i}$ serves as a scaling factor to control the strength of the penalty. This allows flexibility in adjusting how strongly non-uniformity is penalized, as further discussed in Remarks 3.2 and 4.2.
See our response to reviewer KP69 for more discussion on $\sigma$.
- [1] Shin, Y., et al. Improved learning-augmented algorithms for the multi-option ski rental problem via best-possible competitive analysis. ICML, 2023.
- [2] Bamas, E., et al. The primal-dual method for learning augmented algorithms. NeurIPS, 2020.
- [3] Buchbinder, N., et al. Online primal-dual algorithms for maximizing ad-auctions revenue. European Symposium on Algorithms, 2007.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the detailed response. I now understand your main contribution is to provide a competitive ratio for all the parameter region, which seems to be a solid one. Therefore, I increase the score to 3.
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for adjusting their score and would be grateful if they could also update the overall recommendation in the original review. Many thanks! | Summary: This paper investigates the problem of online uniform sampling (OUS), where the goal is to allocate a budget uniformly across unknown decision times. The authors formulate the OUS problem as an online optimization problem and propose randomized algorithms to address it. To evaluate the performance, they consider competitive ratio, consistency, and robustness. The proposed method outperforms previous approaches on real-world data.
---
### update after rebuttal and discussion period
After the rebuttal, I raised my score from 2 to 3, taking into account the positive comments from other reviewers, as I am not familiar enough with the topic to fully assess the contribution and novelty of the paper. However, during the discussion period, I became increasingly skeptical about the problem setting itself. While the authors claim that $\tau^*$ is revealed to the algorithm online, it appears that the only observable information is whether $\tau^*$ has been reached. Moreover, the proposed algorithms seem capable of constructing $p_i$ in advance, without any interaction with the environment, which suggests that the problem is an offline setting. For these reasons, I have decided to maintain my original score.
Claims And Evidence: The general claims appear to be reasonable.
Methods And Evaluation Criteria: The general claims appear to be reasonable, with one exception.
Why we need to consider/define $\lambda$-consistency of algorithms?
If the algorithms are designed to solve OUS problem, it should be $1$-consistent as the definition assume the perfect prediction.
Theoretical Claims: I checked proofs in appendix while I skipped some calculation details.
The followings are my claim on the results of the paper.
### Claim 1. Incomplete Proofs for Lemma 3.1 and Lemma 4.1
Lemmas 3.1 and 4.1 claim that the expected sum of probabilities is bounded by the budget constraint $b$.
However, upon examining the proofs in the appendix, it appears that the authors rely on the following approximation (L643):
$$
b-\frac{b}{e-1}\ln(e-1)+\frac{b}{e} \approx b.
$$
Explicit computation, however, shows that:
$$
b-\frac{b}{e-1}\ln(e-1)+\frac{b}{e} \approx 1.05b > b.
$$
This discrepancy suggests that the current proof does not fully establish Lemma 3.1.
To further investigate, I checked explicit values where similar approximations were used:
- Subroutine 2 (L676): the value is $1.047b$.
- Subroutine 3 is fine.
- Subroutine 4 (L973): the value is $1.07b$.
- Subroutine 5 (L1020): the value is $1.018b$.
- Subroutine 6 (L1085): it seems it depends on the value of $L$, where I am not sure.
Based on these findings, I argue that the current proof does not support the correctness of Lemmas 3.1 and 4.1. A more careful analysis is required to ensure that the budget constraint holds.
---
### Claim 2. Remark 3.3: Conditions on $\sigma$
The proof of Theorem 3.1 introduces $\sigma$ without a clear explanation (though it is mentioned briefly in the main text). In Subroutine 2, the authors argue that the last inequality in L781 holds because the function is increasing with respect to $\beta$.
However, this is only true under the condition, $\sigma \leq b/e$.
Similarly, in Subroutine 3, the same technique is used, which holds only if: $\sigma \leq b/e-b/e^2$.
This follows from the equation (L912):
$$
\frac{b}{e} - \frac{\beta}{e^2} + \frac{\beta}{e^2} - \frac{b}{e^2} + \left(\frac{b}{e} - \frac{b}{e^2} \right)\ln \frac{\beta}{b} -\sigma\ln \frac{\beta}{b} =\frac{b}{e} - \frac{b}{e^2} + \left(\frac{b}{e} - \frac{b}{e^2} -\sigma \right)\ln \frac{\beta}{b}.
$$
For the function to be increasing w.r.t. $\beta\in [b,be]$, the coefficient must be positive, which imposes the condition on $\sigma$.
Thus, it would be beneficial to clarify these constraints explicitly in the proof and revise the description in Remark 3.3.
Experimental Designs Or Analyses: The general claims appear to be reasonable, with one exception.
In the synthetic experiments, the authors provide results for their proposed methods and a naive benchmark algorithm. However, since the learning-augmented algorithm requires a confidence interval as input, one could provide a naive point estimate $\tau^*$ (e.g., $(U+L)/2$) for the heuristic algorithm by Liao et al. (2018). Is there a specific reason why the results from Liao et al. (2018) are omitted in the synthetic experiments, whereas they are included for the HeartSteps V1 dataset?
Supplementary Material: I checked Appendices A-C and skimmed D-F.
Relation To Broader Scientific Literature: I do not have specific idea.
Essential References Not Discussed: I do not have specific idea.
Other Strengths And Weaknesses: ### Strength
- The first randomized algorithm to solve OUS problem by formalizing OUS problem as an online optimization problem.
Other Comments Or Suggestions: ### Suggestion
- Using the same acronym for online uniform sampling and online uniformity scheduling (in Section 5) is confusing. Since the latter is not used frequently, it would be better to remove it.
- When the proof relies on the increasing/decreasing property of a function, it would be better to rewrite the equations explicitly to make these properties clear. For example, it is not straightforward to verify in L703 and L898.
- The current lines in figures are thin.
Questions For Authors: Q1. See Methods And Evaluation Criteria
Q2, Q3. See Theoretical Claim section
Q4. See, Experimental Designs Or Analyses section
Q5. What is the role of randomness of $\text{Int}\tilde{\tau}$ in algorithms? Its value can change at each time step, but by at most 1.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's feedback. Below we address each point in detail to further clarify and strengthen the paper. We have also included SeqRTS as a benchmark in the synthetic experiments. We would be happy to provide further clarification if needed.
- **The need for consistency** While perfect predictions ($U = L = \tau^*$) could theoretically achieve $\text{OPT}(\tau^*)$, most learning-augmented algorithms sacrifice 1-consistency to maintain robust across prediction uncertainties [1,2]. Regardless of the confidence interval width, the algorithm must ensure an acceptable worst-case guarantee. Although a separate algorithm could be designed for perfect predictions, consistency measures performance as prediction accuracy improves. In contrast, our algorithm is designed to achieve 1-consistency.
- **Proof of Lemmas 3.1 and 4.1** Sorry for the sloppiness in the proofs. To ensure exact satisfaction of $\mathbb{E}\left[\sum_{i=1}^{\tau^*} p_{i}\right] \leq b$, one can appropriately scale the input budget $b$ in Algorithms 1 and 2. For example, for Subroutine 2, the input budget should be set as $b/1.047$. In our experiments, we have implemented this adjustment to guarantee that the budget constraint is strictly satisfied. We will revise the statement of the lemmas and theorems to reflect this.
- **$\sigma$ in proof of Theorem 3.1** We have revised the text at line 139, c2 to clarify that $\sigma$ acts as a tunable parameter in the penalty term $\sigma \cdot \ln \frac{\max_i p_i}{\min_i p_i}$, scaling the penalty strength to flexibly adjust non-uniformity penalization. We have revised the proof and modified the description in Remark 3.3 accordingly to incorporate the condition on $\sigma$:
>In Appendix C.2, we show that for Subroutine 1, Theorem 3.2 holds over a wide range of $\sigma$ values, specifically $\sigma \leq \frac{2b(\ln(e-1)-1+1/(e-1))}{\ln b+2-2\ln(e-1)}$.
For Subroutine 2, Theorem 3.2 remains valid when $\sigma \leq \frac{b}{e}$. For subroutine 3 where $\tau^*$ can be unbounded, the theorem holds for $\sigma \leq \frac{1}{2-\ln(e-1)} \frac{1}{e}\left(1-\frac{1}{e}\right)^{j^*+1} b$, ensuring that the penalty term scales similarly to the budget term in the objective.
We clarify that for subroutine 3, only requiring $\sigma \leq b/e-b/e^2$ is not enough for the case where $j^*\geq1$. The stronger condition is necessary to maintain a valid competitive ratio via the monotonic property; otherwise, the competitive ratio may become arbitrarily small.
- **Including SeqRTS on synthetic data** Thank you for the suggestion. We have now conducted additional synthetic experiments using the SeqRTs algorithm proposed by Liao et al. (2018) with the suggested naive point estimate $(U+L)/2$. The results are provided on https://imgur.com/a/Vs7nDAu. The results suggest that SeqRTS, in general, performs worse compared to our algorithms.
- **The role of randomness of Int $\tilde{\tau}$ in algorithms** Taking Algorithm 1 as an example, $\text{Int} \tilde{\tau}$ determines whether the current risk time $i$ exceeds the length of the current stage, thereby indicating whether the budget should be updated. Because stage lengths must be integer-valued, $\tilde{\tau}$ must be rounded. To avoid rounding error, we adopt a stochastic rounding method, ensuring that the expectation of the rounded stage length, $\text{Int} \tilde{\tau}$, matches exactly the original value $\tilde{\tau}$. We will further clarify this in our revised paper.
Thank you for catching the typo on online uniform scheduling and suggestions on the figure. We have revised our paper accordingly. Additionally, we will explicitly explain in our proofs the steps that rely on the monotonicity of the functions. Thank you for the suggestion.
- [1] Bamas, E., Maggiori, A., \& Svensson, O. (2020). The primal-dual method for learning augmented algorithms. NeurIPS.
- [2] Kevi, E., \& Nguyen, K. T. (2023). Primal-dual algorithms with predictions for online bounded allocation and ad-auctions problems. International Conference on Algorithmic Learning Theory.
---
Rebuttal Comment 1.1:
Comment: I appreciate the authors' efforts in addressing my concerns, particularly the theoretical analysis. Most of my initial questions and concerns have been resolved in the rebuttal.
While I am not fully confident in assessing the contribution and novelty of this paper due to my limited knowledge to this field, I increased my score to 3, taking into account the comments from other reviewers. | Summary: The topic of this paper is online uniform sampling problem (OUS) - motivated by applications in digital health.
OUS problem is to distribute a sampling budget b uniformly across unknown decision times in horizon [1,T]. An adversary chooses a value tau* in interval [b,T], revealed only online. At each decision time i ∈ [τ*], the goal of the algorithm is to determine a sampling probability to (i) maximize budget spent and (ii) achieve a distribution over tau* that is as uniform as possible.
The paper obtains a randomized algorithm for OUS; it also extends it to incorporate predictions (intervals for tau*), say, LA-OUS (for learning-augmented). The paper shows LA-OUS is consistent and robust.
There are synthetic data experiments showing the performance of OUS and LA-OUS. There is also an experiment on HeartSteps mobile application, which also shows the algorithms work well.
Claims And Evidence: Looks good.
Methods And Evaluation Criteria: Looks good.
Theoretical Claims: Looks good.
Experimental Designs Or Analyses: Looks good. One real-world dataset is a bit unsatisfactory but it is conceivable that the datasets are limited for this problem.
Supplementary Material: Some of the proofs and experimental details.
Relation To Broader Scientific Literature: The paper studies OUS through the lens of online algorithms and competitive analysis.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths
+ A principled approach to the OUS problem
+ Technically nice and non-trivial
Weaknesses
- Very niche application and not sure how broadly this problem occurs
- The lack of good upper bounds is a negative
- The case splitting resembles the one in Shin et al (ICML) - it will be good to clarify what is common and what is different. I agree the settings seem different, but how come there is some similarity in the analysis/three regimes?
Other Comments Or Suggestions: The model has to be spelled out precisely: for each time i in [1, T], what happens and what is the response.
l118 c1: explain ", which is revealed to the algorithm online."
153 c1: why is "penalizing change in treatment probabilities within each level" a useful constraint wrt the "uniform" objective?
The second term in the optimization problem in l153 - why not measure the L1 distance to uniform? That is \sum_i | p_i - b/\tau^*| - Why this particular objective?
l110 c2: what is the randomness in the algorithm?
l204 c1: for consistency, what is the smooth tradeoff on the competitive ratio, as a function of (U-L)?
l229 c1: is j maintained as state in subroutine 2/3 - please clarify?
Is there a scenario where it does not make sense to utilize all budget?
line 332 col 2: typo (in Algorithm 2). similar typos in a few other places (eg, line 312 col 2)
line 321 col 2: what is the competitive ratio averaged over?
some text repeated between regular and learning-augmented setting - wonder if the text can be crisper
Questions For Authors: Is it possible to generalize your algorithms to weighted risk times - each risk time i has a different weight w_i, with the definitions naturally extended to this setting?
Could you obtain stronger bounds if you are allowed to relax the budget a bit? Some type of bicriteria setting.
Synthetic experiments: in addition to uniform at random choice for risk times, could you try some other distribution. Eg, geometrically spaced at the beginning or at the end?
Is the three operating regime inherent or is it an analysis artifact?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the positive review and are glad that the reviewer found our work as "a principled approach to the OUS problem and technically nice and non-trivial."
- **Weighted risk times:** Weighting risk times differently implies varying risk levels, prioritizing higher-risk times. Our approach can naturally handle this by decomposing the problem into independent subproblems for each risk level, see Appendix A.
- **Stronger bounds by relaxing budgeting:** Relaxing the budget constraint is unlikely to improve upper bounds for OUS. Our proof, using Yao's lemma, constructs a hard instance where all feasible deterministic algorithms perform poorly. Slightly relaxing the budget would not yield large improvements. A similar observation applies to the lower bound, where the budget already holds only in expectation. Further relaxation would make the constraint ineffective.
- **Distribution of $\tau^\star$ in experiments:** Our proposed algorithms are, by design, independent of the specific distribution of risk times. They determine intervention probabilities solely based on the number of risk times $\tau^*$. Thus, for a fixed $\tau^*$, the results remain the same whether the risk times are uniformly distributed or geometrically spaced.
- **Case splitting compared with Shin et al/three regime inherent or analysis artifact?** While Shin et al. proposed a single unified randomized algorithm without different regimes, providing guarantees as $T\rightarrow\infty$, we focus on finite-horizon guarantees under the additional budget constraint $b$. For example, our Algorithm 1 considers three regimes: 1) $T \leq be$ (Subrt 1), 2) $be < T \leq be^2$ (Subrt 2), and 3) $T > be^2$ (Subrt 3). Case 3 resembles Shin et al.'s infinite-horizon setting, where both $T$ and $\tau^*$ can be unbounded. However, our budget constraint introduces new challenges, necessitating novel algorithm design. In Case 3, to meet the budget constraint, the algorithm must initially adopt a conservative approach, resulting in a slightly lower competitive ratio. To mitigate this, we introduce specialized algorithms (Subrts 1 and 2) for the first two regimes, achieving higher competitive ratios. Conversely, both Shin et al.'s *proof* and ours rely on a case-by-case analysis to evaluate the robustness of the learning-augmented algorithm, as computing the expected cost depends on identifying the phase in which the algorithm terminates. We will add the above clarification to our revised paper.
- **Model must be spelled out precisely:** We revised L81 c2 as follows:
>At each decision point $t\in[1, T]$, the algorithm observes the binary risk level $R_t$ associated with the patient. Here, $R_t=1$ indicates a heightened likelihood of an adverse event, such as a relapse into smoking, while $R_t=0$ implies a lower risk level.
- **l118 c1** We revised L93 c2 as follows:
>Since $R_t$ is revealed to the algorithm online, the total number of risk times throughout the decision period, $\tau^* = \sum_{t=1}^T R_t$, remains *unknown* until the last decision point $T$.
- **153 c1 L1 distance in penalty term:** Our choice of penalty ties to the uniform constraint through the two primary objectives outlined in Section 2.1 L122-124. Other alternative penalty terms that satisfy the properties described in Remark 2.1 could also be considered. However, the proposed L1 distance penalty is not appropriate, as it does not sufficiently penalize cases where probabilities are zero ($p_i=0$), which can result in budget depletion before the final risk time.
- **l110 c2** The randomness of the algorithm comes from the initialization step, where $\alpha\in [b,be]$ is sampled from a distribution with probability density function $f(\alpha) = 1/\alpha$. This sampled value $\alpha$ is subsequently used to calculate treatment probabilities. We have further clarified this point on L210.
- **l204 c1 consistency tradeoff:** Consistency, as defined in L195, is defined relative to a perfect prediction of the risk times, i.e., when $U=L=\tau^*$. Thus, there is no trade-off between consistency and prediction interval width $U-L$. Our algorithm achieves 1-consistency. Further discussion on consistency is included in our response to Reviewer KP69.
- **l229 c1 on j:** $j$ acts as a stage counter, incrementing when $i > \text{Int}\tilde{\tau}$ and triggering a budget update when $j>3$ to avoid budget depletion before the final risk time. For each problem instance is assigned to a specific subroutine based on $T$, separate counters $j_1$ and $j_2$ for Subrts 2 and 3 are unnecessary.
- **Not using all budget:** While full budget utilization is ideal for inference, given that $\tau^*$ is random, achieving this under uniform constraints is hard in practice.
- **l321 c2** We revised l321c2 as follows:
> The evaluation metric is the average competitive ratio computed from 500 experimental replications.
Thank you for catching the typo and redundant texts. These have been fixed. | null | null | null | null | null | null |
PTTA: Purifying Malicious Samples for Test-Time Model Adaptation | Accept (poster) | Summary: The paper presents PTTA, a plug-and-play method for purifying malicious (unhelpful) samples for test-time adaptation.
PTTA selects benign samples by comparing the samplewise gradients.
Instead of simply filtering out malicious samples, PTTA transforms them into benign samples via Mixup with benign samples.
PTTA results in high accuracy improvements over various scenarios.
## update after rebuttal
The rebuttal addressed some of my concerns, including insufficient experiment results and computational complexity, so I raised the score from 1 to 2. However, I still worry (1) the problem (malicious sample hazard) is straightforward and (2) the solution lacks novelty.
Claims And Evidence: 1. The claim on the entropy-accuracy relationship is straightforward, but the literature (e.g., EATA) has partially discussed it.
1. The paper's key claims about PTTA's effectiveness are generally supported by the experimental evidence.
Methods And Evaluation Criteria: 1. Please consider revising the manuscript regarding the methods. The current manuscript lists various approaches for saliency indicators, benign sample retrieval, and purification methods. It is unclear which version PTTA is using in the main experiments. Please improve the claims to support the best-working approach.
1. The evaluation setting of datasets aligns with standard benchmarks in the TTA field.
1. The experiment does not include the evaluation of computational overhead (e.g., memory, latency) with and without PTTA.
Theoretical Claims: There are no novel theoretical claims that need to be checked.
Experimental Designs Or Analyses: The paper experimented with full TTA (single) and continuous TTA (continuous) settings with various datasets, including ImageNet-C. Baselines include TENT, EATA, DeYO, and CPL.
Issues:
1. It is not specified why PTTA is not applied to CoTTA and SAR in Tables 2 and 3.
1. TENT is missing in Table 2.
1. It is unclear why ETA is used as the baseline in Table 1 instead of EATA.
Supplementary Material: I checked the supplementary materials, including the gradient derivations, pseudo-code, implementation details, and experiment results.
Issues:
1. Inconsistent evaluations with MedBN—In Tables 12 and 13, some evaluations are PTTA applied within MedBN, and some are not.
Relation To Broader Scientific Literature: PTTA can be applied in broader scenarios where test sample quality is low or includes noisy samples.
Essential References Not Discussed: 1. The paper does not discuss SoTTA [a] as a baseline, which robustly adapts to noisy data streams.
[a] Gong, Taesik, et al. "SoTTA: Robust Test-Time Adaptation on Noisy Data Streams." NeurIPS 2023.
Other Strengths And Weaknesses: Minor Weakness
1. The technical novelty of sample purification is just a simple mixup technique, limiting the novelty.
1. Using source training data for in-distribution retrieval might limit the applicability.
Other Comments Or Suggestions: 1. Please thoroughly check the citations. A few citations lack published years (e.g., Lee et al., Chen et al.).
Questions For Authors: 1. As stated in the abstract, sample purification is the main novelty of the paper, but purification is just a simple Mixup, limiting its novelty.
1. It is unclear which method will be the final method for PTTA. The current manuscript lists the potential methods and shows the ablation study. The writing should be improved to better convey the current method's importance.
1. The experiment is inconsistent across the evaluations. Please answer the concerns in the experimental setting.
1. Please report the computational overhead compared to the baselines (with and without PTTA).
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate the time and effort put into reviewing our paper and providing valuable feedback. We would like to address your questions below and provide a link to figures and tables.
[link] https://anonymous.4open.science/r/PTTA/tab_fig.pdf
> **R4Q1**: On the claim on entropy-accuracy relationship.
We clarify that the entropy-accuracy relationship discussed in Sec. 3.1 is employed to demonstrate the **malicious sample hazards** in TTA methods. Our primary objective is to emphasize that directly utilizing malicious samples for TTA would undermine the stability of DNNs. Additionally, in contrast to EATA, we further demonstrate empirically that test data distributions with higher average entropy exhibit lower overall accuracy (Fig. 3 (down)), which is validated across both ResNet and ViT.
> **R4Q2**: The key claims about PTTA are generally supported by the experimental evidence.
We also provide a theoretical justification for PTTA. Please refer to **R2Q2** for details.
> **R4Q3**: It is unclear which version of PTTA is used in the main experiments.
We clarify that the default version of PTTA employed in the main experiments (**logit-saliency indicator & OOD retrieval**) is detailed in the **implementation part of Sec. 4.1** (lines 304–329). We hope it can address your concerns.
> **R4Q4**: On the evaluation of computational overhead.
We provide comparative analyses of **running times** between different TTA methods and their PTTA-applied versions, along with **quantified storage overhead** for PTTA's memory bank. Please refer to **R1Q1** for details.
> **R4Q5**: Issues on experimental designs and analyses.
We conduct experiments applying PTTA to CoTTA and SAR in Table C of [link], the results support our claims. We clarify that ETA, DeYO, and CPL were **selected as representative sample-selection-based TTA methods**. Due to EATA's foundational version ETA is **entirely based on sample selection**, so ETA is more suitable to be a baseline. Also, EATA use a Fisher regularizer measured in source domain, which is not source-free.
> **R4Q6**: On some missing experimental results.
We provide results for Tent on lifelong TTA task in Table C of [link], and MedBN+PTTA for adversarial defense on ImageNet-C in Table G of [link]. MedBN relies on a large batch size, which underperforms BN Adapt for adversarial defense. Therefore, BN Adapt+PTTA achieves the best performance on ImageNet-C for adversarial defense.
SoTTA [1] was not selected as a baseline since its sample selection criterion aligns with CPL (Zhang et al., 2024), as both aim to maintain uniform class sampling. Additionally, CPL is a new state-of-the-art method in this field. However, we also provide a comparison with SoTTA [1] in Table C of [link]. We hope these studies can address your concerns.
[1] Gong, et al. Sotta: Robust test-time adaptation on noisy data streams. In NeurIPS, 2023.
> **R4Q7**: On the novelty of this paper.
We emphasize that the main contributions of this paper include: 1) analysis of **malicious sample hazards** in TTA tasks, 2) a **saliency indicator** to effectively encode benign and malicious data, and 3) a **plug-and-play PTTA framework** for malicious sample purification.
While PTTA employs Mixup technique, we clarify that **vanilla Mixup alone proves ineffective for TTA methods**. PTTA's effectiveness fundamentally stems from our proposed purification strategy and framework.
Notably, PTTA uses OOD retrieval by default **without requiring any source data**.
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. I appreciate the updates on experimental settings and results.
In terms of the novelty, an analysis of malicious sample hazards is not surprising. They can be easily inferred by the nature of entropy.
Also, I found that PTTA results in about 40% increase in running time. Backpropagation on each sample for the saliency indicator must be a substantial computational burden. Could you specify the testing environment?
---
Thank you for the quick response. I will increase the score and keep track of other reviewers' discussions to adjust the score further.
---
Reply to Comment 1.1.1:
Comment: Thank you for your professional feedback. We provide further explanations below.
We would like to highlight that directly using malicious samples for TTA undermines the stability of DNNs, which **constitutes only one aspect of our analysis regarding malicious sample hazards**. Furthermore, we demonstrate that malicious samples are incorporated into mini-batches at uncertain proportions. **Existing sample selection criteria (employed in ETA, DeYO, CPL, etc.) fail to completely eliminate malicious samples from test data**. These criteria also exhibit **high sensitivity to threshold values** (typically treated as hyperparameters), where slight variations would lead to significant performance degradation, as illustrated in Fig. 2. Such limitations constrain the practical utility of sample-selection-based TTA methods across diverse tasks and scenarios, forming **another dimension of our analyzed malicious sample hazards** (lines 149-163). Consequently, rather than designing selection criteria to filter out malicious samples, we propose the purification strategy to transform malicious samples into benign ones.
Regarding the running time, we clarify that the logit-saliency indicator (default in our PTTA) introduces **no additional gradient backpropagation** beyond base TTA algorithms. Instead, we explicitly compute this indicator through **Eq. 4**, which involves only **lightweight operations** (dot product and element-wise multiplication/subtraction) between two C-dimensional vectors (where C denotes the number of classes), making it **highly efficient**. Consequently, the logit-saliency indicator **converts a gradient-based method into a forward-only solution**, which is recognized by Reviewer iMq6. For comprehensive verification, Table 1 compares the forward/backward passes between base TTA methods and their PTTA-applied versions, while Appendix B.1 provides theoretical derivations for the logit-saliency indicator.
Additionally, we specify the testing environment for evaluating the running time:
**Hardware**: CPU: Intel® Xeon® Silver 4210 @ 2.20GHz | GPU: NVIDIA GeForce RTX 3090 | RAM: 256GB
**Software**: PyTorch 1.9.0 | CUDA 11.1
All experiments are conducted on a single GPU without Automatic Mixed Precision (AMP), with the following exceptions: 1) CoTTA \& CoTTA+PTTA utilize AMP by default, 2) CoTTA \& CoTTA+PTTA for ViT-B/16 employ dual GPUs via Distributed Data Parallel (DDP).
We sincerely hope our clarifications above can improve your opinion of our work and can help you reconsider your score.
Best Regards
----
We are glad that our explanations are helpful in improving your opinion of our work. Thank you again for your expertise and invaluable feedback in enhancing the quality of our paper!
Best Regards | Summary: The paper introduces a method called Purifying Malicious Samples for Test-Time Model Adaptation (PTTA), a plug-and-play solution. Instead of filtering out, the authors identify that malicious samples in test data, though reflecting the data distribution, can undermine the stability of TTA algorithms. To address this, PTTA aims to transform malicious test samples into benign ones. It uses a saliency indicator to encode the impacts of benign and malicious samples on TTA, and retrieves benign samples with opposite contributions to the objective function compared to malicious samples. And then, the Mixup technique is employed for sample purification. Extensive experiments under various scenarios demonstrate that PTTA improves the performance of existing TTA methods.
Claims And Evidence: Instead of filtering out, the authors identify that malicious samples in test data, though reflecting the data distribution, can undermine the stability of TTA algorithms. To address this, PTTA aims to transform malicious test samples into benign ones. Extensive experiments under various scenarios demonstrate PTTA improves the performance of existing TTA methods, validating the claim.
Methods And Evaluation Criteria: PTTA aims to transform malicious test samples into benign ones. It uses a saliency indicator to encode the impacts of benign and malicious samples on TTA, and retrieves benign samples with opposite contributions to the objective function compared to malicious samples. And then, the Mixup technique is employed for sample purification. Evaluations are also reasonable with experiments show that PTTA improves the performance of existing TTA methods under various scenarios.
Theoretical Claims: The proof of logit-level saliency indicator is insightful, transforming a gradient-based method to a forward only solution.
Experimental Designs Or Analyses: Upon inspection of the experimental designs, I find them to be reasonable. The utilization of a diverse range of benchmarks offers comprehensive experimental support, effectively validating the proposed approach's efficacy.
Supplementary Material: N/A
Relation To Broader Scientific Literature: Most of previous TTA methods focused on filtering out malicious samples in the test data. The authors, however, pointed out that instead of simply discarding them, these malicious samples can potentially undermine the stability of TTA algorithms. Their approach is to transform these malicious samples into benign ones. Through comparisons with existing techniques such as the FGSM, the advantages of the proposed PTTA method are demonstrated.
Essential References Not Discussed: Comparing PTTA to diffusion-based malicious-to-benign sample transformation methods (Gao et al., 2024) would strengthen the evaluation.
[Gao’24] Gao, Jin, et al. "Back to the source: Diffusion-driven adaptation to test-time corruption." CVPR. 2023.
Other Strengths And Weaknesses: ## Strengths:
1. The paper addresses a significant issue in TTA by focusing on malicious samples. PTTA's approach of transforming rather than discarding them, along with its non-sensitive threshold nature, makes it suitable for TTA scenarios, demonstrating innovative thinking.
2. The detailed experiments comprehensively validate PTTA across various settings like continual, lifelong, and adversarial, also with VLM backbones. Its excellent performance on multiple benchmarks and plug-and-play feature strongly prove its effectiveness, which is commendable.
3. The paper's explanation of the logit-level saliency indicator is profound. Converting a gradient-based method into a forward-only solution showcases technical sophistication.
4. The paper is written in a smooth and easily understandable manner.
## Weaknesses:
1. The paper lacks quantification of the memory and computational overhead comparison between the original methods and when PTTA is incorporated. For a plug-and-play method, especially in the TTA field, such quantification is important. It would help better understand its practicality and broad applicability in different resource-constrained environments.
2. Although PTTA has been well-validated in several scenarios, it would be better to verify whether it is effective when combined with teacher-student structure methods like COTTA. Also, comparing PTTA to diffusion-based malicious-to-benign sample transformation methods (Gao et al., 2024) would strengthen the evaluation.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate the time and effort put into reviewing our paper and providing valuable feedback. We would like to address your questions below and provide a link to figures and tables.
[link] https://anonymous.4open.science/r/PTTA/tab_fig.pdf
> **R3Q1**: The paper lacks quantification of the memory and computational overhead comparison.
We provide comparative analyses of **running times** between different TTA methods and their PTTA-applied versions, along with **quantified storage overhead** for PTTA's memory bank. Please refer to **R1Q1** for details.
> **R3Q2**: It would be better to verify whether PTTA is effective when combined with teacher-student structure methods.
We conduct experiments applying PTTA to two teacher-student structure methods, i.e., **CoTTA and CTDA [1]**, with results presented in Table C of [link]. These demonstrate that PTTA effectively enhances the performance of teacher-student structure TTA methods.
[1] Wang, et al. Continual test-time domain adaptation via dynamic sample selection. In WACV, 2024.
> **R3Q3**: On comparison between PTTA and diffusion-based malicious-to-benign sample transformation methods.
We provide comparative experiments between PTTA and Diffusion-based DDA [2] when applied to base TTA methods (ETA, DeYO, and CPL) in Table D of [link]. The results show that Diffusion-based DDA **significantly degrades the performance of base TTA methods in some cases**, while incurring **prohibitive computational overhead** (requiring $4\times 4090$ GPUs and approximately 45 hours to complete an experiment for a single corruption type), rendering Diffusion-based DDA impractical for TTA tasks.
[2] Gao, et al. Back to the source: Diffusion-driven adaptation to test-time corruption. In CVPR, 2023. | Summary: Existing TTA algorithms often focus on selecting benign samples for self-training, which leads to wasted test data. To address this, the authors propose PTTA, which uses a saliency indicator to identify benign samples with opposing effects on the objective function and combines them with malicious samples via Mixup. This strategy effectively leverages the information in malicious samples, improving online test accuracy. Extensive experiments across four TTA tasks, as well as classification, segmentation, and adversarial defense, validate the method’s effectiveness.
Claims And Evidence: The claims made in the submission seem to be supported by clear and convincing evidence. However, in the ablation study section, the author states that “as K approaches infinity, it will dilute the proportion of original data information in purified samples.” This conclusion, however, cannot be directly drawn from Figure 9. Furthermore, what would be the result if the harmful samples were directly removed and only the corresponding benign samples were used in the Mixup? Rather than the fact that using more samples can improve TTA performance, I am more interested in understanding why the samples generated by Mixup on the original samples are effective.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand.
Theoretical Claims: I did not check the correctness of proofs for theoretical claims.
Experimental Designs Or Analyses: The experiments in the paper are thorough, covering four types of TTA tasks as well as classification, segmentation, and adversarial defense, with well-executed analysis of the results.
Supplementary Material: The author did not provide supplementary material, but a GitHub link is provided where the code for the method can be found.
Relation To Broader Scientific Literature: Mixup is a commonly used data augmentation technique, and the author applies it to malicious samples in TTA to achieve higher sample utilization.
Essential References Not Discussed: Work [1] applies mixup to test-time training to prevent performance degradation in the main task and mitigate the mismatch problem. Work [2] improves sample utilization by performing negative learning through complementary labels. I believe these works share similarities with the ideas presented in the paper, and the authors should discuss it further to better highlight the key contributions of the work.
[1] Mixup for Test-Time Training. arXiv:2210.01640
[2] Continual Test-time Domain Adaptation via Dynamic Sample Selection. WACV 2024
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: See above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate the time and effort put into reviewing our paper and providing valuable feedback. We would like to address your questions below and provide a link to figures and tables.
[link] https://anonymous.4open.science/r/PTTA/tab_fig.pdf
> **R2Q1**: What's the results of purifying only begin samples?
We present an ablation study in Table F of [link] comparing PTTA and direct removal of malicious (harmful) samples with purification of benign samples via Mixup. The results indicate that purifying only benign samples yields performance improvements of base TTA methods. Furthermore, additionally leveraging information from malicious samples via PTTA further enhances the performance.
> **R2Q2**: Why is Mixup for PTTA effective?
In general, Mixup helps enhance model robustness against adversarial attacks and improves generalization on out-of-distribution data [1]. It has also been demonstrated to refine the calibration of DNNs and mitigate overfitting [2].
Next, we perform a Taylor expansion of the purification loss (Eq. 7) at mixup ratio $\lambda$ equals 0:
$$
\mathcal{L}\_{pur}(x^-, x^+) = - (\lambda y^- + (1-\lambda)y^+)^T \log f(\lambda x^- + (1-\lambda) x^+)
= -(\lambda y^- + (1-\lambda)y^+)^T\log f(x^+) + \lambda (x^- - x^+) \nabla\_{x^+} \mathcal{L}\_{ce}(f(x^+)) + \mathcal{O}(\lambda^2),
$$
where $x^-$ is a malicious sample, $x^+$ is a benign sample, $y$ is an output vector, $f$ denotes the model, $\mathcal{L}\_{ce}$ is the Cross-Entropy loss.
Minimizing $\mathcal{L}\_{pur}(x^-, x^+)$ reduces the loss of $-(\lambda y^- - (\lambda-1)y^+)^T\log f(x^+)$ while mitigating the interference of perturbations on $x^+$ to the predictions of $f(x^+)$, thereby enhancing model robustness. Large differences between $x^-$ and $x^+$ could enhance the influence of the first-order term in $\mathcal{L}\_{pur}(x^-, x^+)$, which verify the necessity and effectiveness of our proposed benign sample retrieval.
Furthermore, we provide intermediate continual test-time adaptation process in Figure A of [link], empirically validating the effectiveness of using Mixup for PTTA.
[1] Zhang, et al. How does mixup help with robustness and generalization? In ICLR, 2021.
[2] Thulasidasan, et al. On mixup training: Improved calibration and predictive uncertainty for deep neural networks. In NeurIPS, 2019.
> **R2Q3**: On the claim of $K$ in the ablation study.
Due to the lack of clear trends in Fig. 9, please refer to Table 14 for detailed results, which demonstrate that as $K$ approaches infinity, it will dilute the proportion of original malicious data information in purified samples. Because we set $λ=1/(K+1)$, as $K$ approaches infinity, $\lambda$ approaches 0, causing $\mathcal{L}\_{pur}(x^-, x^+)$ to degenerate into $\mathcal{L}\_{ce}(f(x^+))$, thereby reducing PTTA to base TTA methods that remove all malicious data information.
> **R2Q4**: On comparison with works [3] and [4].
Work [3] mixes test samples with randomly selected training samples to perform an auxiliary task, which is designed for auxiliary test-time training and diverges significantly from the TTA framework.
Work [4] employs negative learning to improve the utilization of malicious data. However, purification strategy-based PTTA outperform work [4] in TTA tasks, as validated in Table C of [link].
[3] Zhang, et al. Mixup for Test-Time Training. arXiv:2210.01640.
[4] Wang, et al. Continual test-time domain adaptation via dynamic sample selection. In WACV, 2024.
---
Rebuttal Comment 1.1:
Comment: Thanks to the author’s reply, most of my concerns have been resolved, and I will adjust my score accordingly.
---
Reply to Comment 1.1.1:
Comment: Thank you for upgrading your score and the expertise and invaluable feedback in enhancing the quality of our paper!
Best Regards | Summary: This paper focuses on leveraging malicious samples during Test-Time Adaptation (TTA) to improve data utilization. The authors propose PTTA, a plug-and-play method that retrieves benign samples with maximal divergence from malicious samples and employs a Mixup strategy to purify malicious samples for TTA. PTTA demonstrates compatibility with existing TTA methods, and extensive experiments validate its effectiveness across multiple datasets, backbones, and tasks.
## update after rebuttal
My concerns have been addressed. I think this paper can be accepted now. This paper provides a valuable exploration of malicious sample utilization in TTA, with extensive experiments validating the effectiveness of the proposed method. In my opinion, this work is well-executed and deserves acceptance. To further strengthen the contribution, I would suggest extending the discussion that could provide deeper insights for readers.
First, it would be further improved by including a brief discussion with more TTA approaches. The paper could consider some of the recent TTA methods, such as FOA [1], ROID [2], MGTTA [3] and EATA-C[4]. Unlike this work, these methods do not perform purification on malicious samples but instead design general optimization strategies using all samples, achieving significant performance improvements as well. Second, some studies explore enhancing TTA performance from the perspective of improving TTA process. For example, improving entropy loss [5-6], refining batch normalization[7], and optimizing the inference process [9]. Third, the paper primarily discusses the application of TTA in image classification and semantic segmentation. It would be worthwhile to explore whether the proposed method can be extended to other domains and tasks, such as image super-resolution [9], video classification [10-11], and visual question answering [12].
[1] Test-Time Model Adaptation with Only Forward Passes, ICML 2024.
[2] Universal test-time adaptation through weight ensembling, diversity weighting, and prior correction, WACV 2024.
[3] Learning to Generate Gradients for Test-Time Adaptation via Test-Time Training Layers, AAAI 2025.
[5] TEA: Test-time Energy Adaptation, CVPR 2024.
[6] Decoupled Prototype Learning for Reliable Test-Time Adaptation, arXiv 2025.
[7] Unraveling batch normalization for realistic test-time adaptation, AAAI2024.
[8] Boost test-time performance with closed-loop inference, arXiv 2022.
[9] Efficient test-time adaptation for super-resolution with second-order degradation and reconstruction, NuerIPS 2023.
[10] Video Test-Time Adaptation for Action Recognition, CVPR 2023.
[11] Exploring Motion Cues for Video Test-Time Adaptation, ACM MM 2023.
[12] Test-time model adaptation for visual question answering with debiased self-supervisions, TMM 2023.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes. I have checked the proof of Logit-saliency indicator.
Experimental Designs Or Analyses: Yes. The experimental design rigorously evaluates common TTA baselines and tasks, with comprehensive validation on diverse benchmarks.
Supplementary Material: Yes. I have reviewed additional implementation details and results.
Relation To Broader Scientific Literature: This paper is closely related to the field of test-time adaptation, sample selection, and the use of malicious samples.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths
1. The paper is well-structured and clearly written.
2. PTTA is a simple yet practical plug-and-play approach, seamlessly integrating with existing TTA frameworks.
3. Thorough ablation studies and evaluations across diverse scenarios (datasets, backbones, tasks) strongly support the method’s efficacy.
Weaknesses
1. Lacks detailed computational complexity analysis. While PTTA improves performance, Table 1 indicates increased time (additional forward passes) and memory costs (memory bank). A critical analysis is missing: How do SOTA methods perform under comparable computational constraints? (For example, maintain a memory bank and randomly select benign samples for adaptation when encountering malicious samples.)
2. Motivation of the proposed method is incomplete. The connection between adversarial purification and the proposed saliency indicator (Sec. 3.2) requires stronger justification. The rationale for linking gradient directions of entropy minimization to noise encoding remains unclear.
Other Comments Or Suggestions: 1. Mixup Rationale: A brief theoretical or empirical justification for using Mixup in Sec. 3.3 would strengthen the methodology.
2. The main text seems to lack a reference and introduction to Figure 1.
Questions For Authors: See the comments above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate the time and effort put into reviewing our paper and providing valuable feedback. We would like to address your questions below and provide a link to figures and tables.
[link] https://anonymous.4open.science/r/PTTA/tab_fig.pdf
> **R1Q1**: Lacks detailed computational complexity analysis.
We provide comparative analyses of **running times** between different TTA methods and their PTTA-applied versions in Table A of [link], along with **quantified storage overhead** for PTTA's memory bank in Table B of [link]. Additionally, Table E of [link] compares state-of-the-art TTA methods with their PTTA-applied versions **under comparable computational constraints**. The results support PTTA's superiority.
> **R1Q2**: Motivation of the proposed method is incomplete.
Adversarial purification methods typically leverage the first-order partial derivatives of the objective loss function with respect to the image $x$, i.e., **the saliency information**: $\gamma = \xi \cdot \text{sign}(\nabla_x \mathcal{L}(f_\theta(x), y(x))$, as an unit vector in the image space for sample purification.
Saliency information quantifies which individual pixels require the most modification to minimize the objective loss function. Consequently, **samples contributing similarly to the objective loss function exhibit aligned directions of their saliency information unit vectors**, resulting in small Cosine distances that serve as the *saliency indicator*.
While Entropy Minimization (EM) is a widely adopted objective loss function in TTA methods, we use EM-derived saliency indicator for noise encoding. Notably, we validate in Table C of [link] that the saliency indicator based on the teacher-student consistency loss function (used in CoTTA and CTDA [1]) also achieves strong efficacy, demonstrating the **flexibility in choosing objective loss functions**.
[1] Wang, et al. Continual test-time domain adaptation via dynamic sample selection. In WACV, 2024.
> **R1Q3**: On a brief theoretical or empirical justification for using Mixup.
We provide a brief theoretical and empirical justification for using Mixup in PTTA. Please refer to **R2Q2** for details.
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Rebuttal Comment 1.1:
Comment: All my concerns have been adequately addressed.
Regarding Question 1: While the method increases forward passes, the authors have now supplemented time cost analysis and performance comparisons under equivalent time constraints.
Regarding Question 2: The motivation clarification in the methodology section has been strengthened with additional explanations and justifications.
I currently have no further questions and recommend maintaining my original assessment.
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Reply to Comment 1.1.1:
Comment: We are delighted to learn that all your concerns have been addressed. Thank you again for your expertise and invaluable feedback in enhancing the quality of our paper!
Best Regards | null | null | null | null | null | null |
LLM-SRBench: A New Benchmark for Scientific Equation Discovery with Large Language Models | Accept (oral) | Summary: The paper introduces a benchmark for scientific equation discovery, where the model are able to use both input/output values along with a problem description in human language, into constructing an equation that describes the data well. The model tested on this benchmark would be measured by the accuracy of the recovered equation and also the semantic accuracy of the equation. From results, normal LLMs are able to perform poorly on this task.
Claims And Evidence: I think based on the paper, it can be shown that LLMs are still unable to properly incorporate scientific information into its predictions, which I think is a fair conclusion from the trial experiments ran with the benchmarks.
Methods And Evaluation Criteria: I think the dataset is quite unique, and it is definitely a good start to other works in this area. Some general comments I have with the proposed dataset are as follows:
- A point that would make the dataset more realistic and fitting of real world scenarios would be incorporation of some observation noise, which is typical when actual experiments are conducted. This could potentially be done through curation of some real experiment data, or can simply be addition of some noise into the training set.
- I notice that the preliminary results are mostly for LLM evaluators, which make sense since the benchmark also include domain knowledge in human language. Despite this, it would be interesting to see how traditional symbolic regression methods would fare on the dataset, even if they are not able to incorporate the domain knowledge. Based on what the metrics from the authors, they may fare well in terms of accuracy but less so in semantic similarity, which would make the need for LLM-based discovery stronger, and the dataset more useful.
Also some comments regarding evaluation criteria:
- I'm not fully convinced with using LLMs to evaluate semantic similarity, also despite the 94.6% figure quoted by the authors whose experimental details are not so clear (e.g., how can we be sure the 130 test cases cover all cases that can be output by an LLM?). I understand that it can be hard to determine semantic similarity, but maybe more classical methods would be applicable if the output form of the equations can be more restrictive (which may be against what the authors want though).
- From what I understand, typical SR papers uses R2 score as the evaluation criteria. I'm wondring why this paper does not also include that.
Theoretical Claims: There are none.
Experimental Designs Or Analyses: The results seem okay, but would also benefit from some kind of confidence/score variance value as well. Some issues are with evaluation criteria, which I describe above.
Supplementary Material: I have skimmed the appendix and see no immediate issues. In particular, I had a look at the sample of equations in the benchmarks and the evaluation methods.
Relation To Broader Scientific Literature: I think the paper would have great relevance, since it can be a good step to involve scientific reasoning into modelling data. Even though there are still ways that the benchmark could be improved to be more realistic with the scientific uses, or to incorporate even more equations from more domains within each subfields, but overall it may still be a good start for work in this direction.
Essential References Not Discussed: None that I am aware of.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: None.
Questions For Authors: Most of the questions/suggestions I have additionally can be found in previous sections, and are related to some aspects of the evaluation criteria, and with the realism of the dataset that may be improved.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for dedicating your time and expertise to review our submission. Please find our responses below.
> it would be interesting to see how traditional symbolic regression methods would fare on the dataset... which would make the need for LLM-based discovery stronger, and the dataset more useful.
Thanks for the thoughtful suggestion and constructive feedback. Previous work on LLM-based scientific equation discovery (LLM-SR, LaSR, and SGA) has provided evidence for the benefits of these approaches compared to traditional methods. However, we agree that evaluating traditional non-LLM methods on our benchmark would further demonstrate these advantages.
In response to your suggestion, we conducted experiments with PySR (a state-of-the-art non-LLM baseline) on our benchmark datasets during the rebuttal period. The results (shown in table below) demonstrate that PySR often achieves competitive numeric accuracy but considerably lower symbolic accuracy, particularly on non-physics datasets. This confirms that while traditional methods can fit data numerically, they struggle with symbolic understanding due to lack of domain knowledge. We also think that these findings further motivate the value of LLM-based techniques for scientific equation discovery. Thank you again for the constructive feedback. We will surely include this analysis in the final version.
| Dataset (Metric) | LLM-SR (best) | LaSR (best) | SGA (best) | PySR |
|---------|---------------|-------------|------------|------|
| LSR-Transform (SA / Acc0.1) | 31.53 / 39.64 | 12.61 / 50.45 | 9.91 / 8.11 | 8.11 / 56.76 |
| LSR-Synth Chemistry (SA / Acc0.1) | 11.11 / 66.66 | 2.77 / 38.92 | 0 / 16.66 | 0 / 41.67 |
| LSR-Synth Biology (SA / Acc0.1) | 25.30 / 58.33 | 8.33 / 20.83 | 4.16 / 12.51 | 0 / 25.0 |
| LSR-Synth Physics (SA / Acc0.1) | 9.91 / 36.36 | 9.91 / 31.81 | 4.54 / 9.09 | 4.54 / 29.55 |
| LSR-Synth MatSci (SA / Acc0.1) | 20.24 / 88.28 | 28.12 / 72.04 | 0 / 36.11 | 0 / 68.0 |
**Incoporation of noise** Thank you for the comment. We have not explored the imacpt of noise in the our benchmark's data generation. The main motivation of this benchmark was to help community towards building better general LLM-based equation discovery agents that can be leveraged in scientific domains, addressing the challenges of current benchmarks for the emerging LLM-based techniques.
We fully agree with the reviewer on the importance of noise in real-world scientific discovery scenarios. This is one of the directions we're considering for future benchmark enhancements.
**R2 vs Accuracy to Tolerance** Thanks for raising this important question. Based on our analysis (and some of the previous works [Kamienny et al., 2022; Biggio et al., 2021]), R2 is not a good metric for the evaluation of symbolic regression, particularly if we have large-scale synthetic data with very different output scales.
- R2 can be easily saturated by normalized mean patterns (similar to NMSE), often missing prediction nuances at different scales. This is evidenced by the consistently high R2 scores (above 0.999) achieved by most recent methods in benchmarks like SRBench.
- The accuracy-to-tolerance metric (defined in Section 2.3) aggregates point-wise normalized metrics for each datapoint rather than normalizing mean aggregated scores. It also implements a tolerance threshold for the worst point-wise normalized distance, making evaluation more robust to function behavior nuances (e.g., sudden changes or spikes)
As the goal of symbolic regression is to learn correct underlying mathematical relations, we should care more about these nuances of function numeric behavior as well as the symbolic mathematical alignment which makes accuracy to tolerance a better metric for numeric precision assessment.
**Evaluation of Equation Semantic Similarity with LLMs vs more classical methods** Thank you for the comment. We will surely add more details on equation semantic similarity evaluation in the updated version.
Regarding the question, we think that restricting the outputs of the equations to specific forms for LLM-based equation discovery won’t be a good idea since one of the main benefits of LLMs is their capabilities in programming and code generation which opens new more flexible representations for equation discovery that was not possible with the previous expression tree based methods and their corresponding symbolic evaluations.
While evaluating semantic similarity is non-trivial, our empirical analysis and human study show that LLMs are usually strong at recognizing equation equivalence across different styles and representations. We also think that correlation between symbolic accuracy (computed from GPT-4o) and generalization (computed from OOD data) shown in Figure 6 further support LLMs effectiveness as semantic symbolic evaluators for equation discovery.
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We hope that most of the reviewer’s concerns have been addressed. We’d be happy to engage in further discussions. | Summary: The paper introduces LLM-SRBench, a novel benchmark designed to evaluate the capabilities of LLMs in scientific equation discovery. The key motivation behind the benchmark is to prevent trivial memorization by LLMs, which has been a limitation in existing equation discovery benchmarks. The benchmark consists of 239 equation discovery tasks across 4 scientific domains (physics, chemistry, biology, and material science) and is structured into two different categories:
LSR-Transform: Reformulates well-known physical equations, from the Feynman benchmark, into less common mathematical forms, making it more difficult for LLMs to rely on memorization.
LSR-Synth: Introduces synthetic equations that combine known scientific terms with novel, discovery-driven components, requiring reasoning and data-driven inference.
The paper evaluates multiple SOTA LLM-based equation discovery methods, including LLM-SR, LaSR, SGA, and direct prompting baselines, using both open-source (Llama-3.1-8B) and closed-source (GPT-4o-mini, GPT-3.5) models. To evaluate model performance, the paper also proposes a novel symbolic accuracy metric, using GPT-4o as an evaluator. Symbolic accuracy correlates with out-of-domain (OOD) performance, suggesting that correctly identified symbolic structures contribute to better generalization. The best-performing method achieves only 31.5% symbolic accuracy on LSR-Transform, highlighting the difficulty of the task. Direct prompting (without data-driven reasoning) performs poorly, showing the necessity of data feedback in scientific equation discovery. LLMs struggle with OOD generalization, indicating that discovered equations often fail to extrapolate beyond the training data.
Claims And Evidence: Supported claims:
The following claims are well-supported by empirical evidence provided in the paper:
1) The authors demonstrate that existing equation discovery benchmarks allow LLMs to rely on memorization rather than true discovery by showing significant performance drops when problems are reformulated (Figure 1).
2) The claim that LLM-SRBench is more challenging is well-supported by the low symbolic accuracy scores (Table 1).
3) The evidence for poor OOD generalization is strong, as models show significantly higher NMSE on OOD test sets (Figure 5), reinforcing the difficulty of extrapolation.
Claims That Need Stronger Justification:
The paper provides evidence that generalization performance varies across scientific domains, with chemistry and biology showing a larger performance gap between in-domain (ID) and OOD cases compared to physics and material science. However, the authors do not analyze why this variation occurs. While it is possible that some domains inherently pose more complex challenges for equation discovery, another explanation could be that the dataset design itself contributes to the difficulty, either through the structure of equations, the nature of data distributions, or the frequency of certain mathematical patterns.
A systematic classification of failure cases across different domains would provide valuable insights. Examining where and how models fail—whether due to misidentified variables, incorrect functional forms, or numerical instability—could help determine whether LLMs struggle more in certain disciplines due to intrinsic domain complexity or due to dataset-specific biases. Table 1 and Figure 5 already indicate that different models perform differently across domains, but the paper does not include concrete examples of incorrect outputs or categorize failure modes. A deeper analysis, including sample failure cases and their classification by domain and model type, could reveal whether generalization failures follow a consistent pattern (e.g., do chemistry problems frequently lead to overfitting, while physics problems lead to missing terms?).
To strengthen this point, the authors should consider adding:
- Representative examples of failure cases across domains (e.g., incorrect equations generated by benchmark models).
- A classification of common failure types (e.g., missing terms, incorrect exponents, incorrect dependencies).
- A discussion on whether these errors stem from domain-specific challenges or dataset characteristics (e.g., certain equation structures in some domains being more prone to errors).
Methods And Evaluation Criteria: The paper benchmarks state-of-the-art LLM-based scientific equation discovery methods using three LLM backbones (Llama-3.1-8B, GPT-3.5, and GPT-4o) and evaluates their performance on LLM-SRBench. The evaluation criteria, including novel symbolic accuracy, numerical precision, NMSE, and OOD generalization, are well-aligned with the problem of equation discovery. Additionally, the symbolic accuracy evaluation using GPT-4o is verified against human expert judgments, ensuring reliability in assessing equation correctness.
By comparing LLM-SRBench with existing benchmarks, the authors effectively demonstrate its increased difficulty and reduced sensitivity to memorization. The models evaluated include LLM-SR, LaSR, SGA, and Direct Prompting (DataBlind), providing a comprehensive comparison of different equation discovery approaches.
Theoretical Claims: No theoretical justification is required in this paper, as it primarily focuses on empirical benchmarking rather than formal proofs. The evaluation metrics used, including symbolic accuracy, NMSE, and OOD generalization, are well-defined and appropriate for assessing scientific equation discovery. No issues were found with their formulation or application.
Experimental Designs Or Analyses: The experimental design is sound, with clear methodology and appropriate evaluation metrics. The hyperparameters used for different methods (LLM-SR, LaSR, SGA, and Direct Prompting) are detailed in the appendix, ensuring reproducibility. Each step in the LSR-Transform and LSR-Synth pipelines is well-documented, and the authors provide code detailing the dataset generation and evaluation procedures, further supporting transparency. No major issues were found in the experimental design.
Supplementary Material: All supplementary materials were reviewed, and they are correctly referenced in the main paper. The provided code is well-documented, allowing for reproducibility and verification of the methods. No inconsistencies were found between the supplementary materials and the main text. However, the qualitative analysis of outputs could be expanded with additional examples to provide deeper insights into the behavior of different discovery methods, as detailed in the “Questions For Authors”.
Relation To Broader Scientific Literature: The paper builds on prior work in symbolic regression (e.g., AI Feynman, PySR) and LLM-based scientific discovery, addressing the issue of memorization in existing benchmarks. It extends benchmarks like SRBench and SRSD by introducing LSR-Transform and LSR-Synth, which focus on reasoning beyond recall. The study aligns with recent advances in LLM-guided symbolic regression (e.g., LLM-SR, LaSR, SGA) and contributes a evaluation framework to test equation discovery in a more challenging and diverse setting. By systematically testing LLMs on equation discovery tasks requiring reasoning over data rather than recall, this work helps advance our understanding of LLMs' ability to generalize mathematical structures, a crucial step toward automated scientific discovery, as demonstrated across four domains: physics, chemistry, biology, and material science.
Essential References Not Discussed: No, the paper appropriately cites and discusses the relevant prior work in symbolic regression, LLM-based scientific discovery, and existing benchmarks to the best of my knowledge.
Other Strengths And Weaknesses: The strengths and weaknesses of the paper are thoroughly discussed in the "Claims And Evidence," "Methods And Evaluation Criteria," and "Questions For Authors" sections above. These include the paper’s well-structured benchmark, strong experimental design, and clear evaluation criteria, along with areas needing further justification, such as failure case analysis, novelty verification.
The LSR-Transform dataset is built upon the Feynman benchmark dataset, but the authors introduce transformations and natural language specifications for each reformulated problem, making it more challenging and reducing reliance on memorization. The LSR-Synth dataset aims to incorporate novel synthetic terms into existing equations, creating discovery-driven problems that go beyond simple equation recall. This approach has the potential to be extended beyond the 4 scientific domains used in the paper, making it a valuable resource for broader scientific applications.
Other Comments Or Suggestions: None.
Questions For Authors: • Domain-Specific Generalization Performance
The paper provides evidence that generalization performance varies across scientific domains, with chemistry and biology showing a larger performance gap between in-domain (ID) and out-of-domain (OOD) cases compared to physics and material science. However, it does not analyze why this variation occurs. Could the observed difficulty stem from intrinsic domain complexity, or might it be influenced by dataset-specific factors such as equation structure, data distribution, or frequency of certain mathematical patterns? Systematic classification of failure cases across different domains could help clarify whether these challenges are due to intrinsic scientific difficulty or dataset artifacts? Specifically:
1) Can the authors provide representative examples of failure cases across domains?
2) Would a classification of common failure types (e.g., missing terms, incorrect exponents, incorrect dependencies) help reveal domain-specific trends?
3) Could the authors discuss whether the failure modes observed in different disciplines stem from the nature of scientific equations themselves or from dataset characteristics?
Clarifying this aspect would help determine whether performance disparities across domains are inherent or dataset-driven. Please refer to the "Claims That Need Stronger Justification" section for detailed concerns.
• Novelty Check in LSR-Synth Pipeline
In the LSR-Synth pipeline, the authors use GPT-4o as a novelty evaluator to determine whether a generated equation is distinct from known scientific expressions. However, LLMs may incorrectly classify an equation as novel despite it existing in prior literature. Since model performance on this dataset is poor, it suggests the problems are challenging, but this does not guarantee that the novelty check is reliable.
4) Could the authors justify why asking GPT-4o alone is sufficient for novelty evaluation? Would a secondary human expert review or detailed literature analysis improve the reliability of the novelty check?
5) Given that novelty assessment is crucial for ensuring LSR-Synth problems do not introduce trivial cases, how can the authors ensure that LLM-generated novelty assessments are not biased or incorrect?
• Dataset Size Reduction in LSR-Transform
In Section 2.1 LSR-Transform, the authors state:
"This process yields 111 total transformed equations derived from the 100 original Feynman problems."
The dataset generation pipeline includes steps to increase diversity by selecting a new target variable (Step 2: Select Pivot Variable) and switching the roles of input-output variables (Step 3: Feature-Target Transformation). However, despite this expansion, only 111 transformed equations remain from an original set of 100 Feynman equations.
6) Is this reduction due to eliminations in Step 5 (Solvability Check) or Step 6 (Dataset Refinement)? Could the authors provide a breakdown of the proportion of equations discarded at each stage to better understand why the final dataset size remains close to the original? Understanding this filtering process would clarify how much of the dataset reduction is due to analytical intractability versus imposed constraints on the transformed dataset.
Ethical Review Concerns: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for dedicating your time and expertise to review our submission. Please find our responses below.
> A systematic classification of failure cases across different domains would provide valuable insights. Examining where and how models fail—whether due to misidentified variables, incorrect functional forms, or numerical instability
Thank you for the constructive suggestion. We examined the failure cases during rebutal period and noticed that LLM-based models usually don't fail due to the syntax function errors (such as missing variables or dependencies). Instead, most errors come from incorrect terms or combination of terms within the equations, reflecting mistakes due to semantic aspects of discovery for a given scientific problem. We could not identify a uniform pattern of specific mathematical relations that consistently challenge current discovery methods. We believe this is because LLM-based equation discovery involves a complex interplay of domain knowledge, search capabilities with data-driven feedback, and mathematical manipulation skills. To thoroughly study failure case patterns would require investigating all these dimensions. We agree with the reviewer on the importance of this research direction for future work.
**Representative Failure Examples** Thank you for this suggestion. We will include examples of failure cases for different methods across domains in the camera-ready version.
> The paper provides evidence that generalization performance varies across scientific domains, ... However, it does not analyze why this variation occurs.
Thanks for the thoughtful question. We have explored problem complexity across domains (Figure 10 in Appendix shows the distribution by complexity). While biology and physics problems have similar and slightly higher complexity than other domains, we observe a smaller ID-OOD gap for physics but a larger one for biology in the results. This suggests factors beyond mere complexity are at play (like LLM domain knowledge).
The reviewer raises an interesting point that would require domain-specific analysis beyond our study's scope. Our primary goal is to develop a benchmark that helps the community build better general LLM-based equation discovery agents applicable across domains. More specialized applications would require domain-focused analyses
> Novelty Check...In the LSR-Synth pipeline, the authors use GPT-4o as a novelty evaluator to determine whether a generated equation is distinct from known scientific expressions. However, LLMs may incorrectly classify an equation as novel despite it existing in prior literature. .. this does not guarantee that the novelty check is reliable.
We cannot theoretically guarantee whether GPT-4o evaluation of novelty is reliable, but evaluating novelty is a non trivial task and we think that LLMs (with their vast knowledge about literature) could be a helpful tool for novelty assessment. Our empirical evidence also supports the effectiveness of this approach: the consistently lower performance of discovery methods on LSR-Synth datasets suggests these problems aren't trivial and do contain novel elements (if they were simply known equations, LLM-based discovery models would likely recall them from embedded knowledge and solve them easily). We agree that more rigorous novelty evaluation involving domain experts and specialized scientific literature retrieval tools would enhance the design of benchmark problems. However, this extension would require significant domain knowledge and human expert review which is not feasible for the rebuttal period but valuable for future work.
**Dataset Size Reduction in LSR-Transform** Here is the detailed breakdown of our filtering process in LSR-Transform: After transformation steps in Figure 3 (Step 4), we obtained 471 transformed problems from the 100 original Feynman problems; During the solvability check with sympy (Step 5), 53 problems were discarded, leaving 418 problems; In dataset refinement (Step 6), we only filtered datapoints to ensure they were within the domain of the new transformed equations, without eliminating any equations at this stage. We then filtered out 307 problems due to significantly higher complexity compared to original problems, resulting in the final 111 problems in LSR-Transform. This is to ensure that the challenging nature of LSR-Transform stems from semantic aspects of discovery rather than from syntactically more complex or lengthy problems (as shown in Figures 4 and 8). We will clarify this process further in the revised version of paper.
**Additional Qualitative Examples of Outputs** As some reviewers have higlighted examples of Figure 14 helpful, we plan to include more hypothesis examples from different domains in the revision of paper.
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We hope that most of the reviewer’s concerns have been addressed. We’d be happy to engage in further discussions.
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Rebuttal Comment 1.1:
Comment: The authors have addressed most of my concerns appropriately. Their explanation of the dataset size reduction in the LSR-Transform pipeline was helpful, clarifying the multi-stage filtering process and their rationale behind discarding high-complexity equations. The inclusion of representative failure cases and qualitative outputs in the camera-ready version also responds to my suggestions for deeper insight into model behavior. The authors mentioned that they plan to include more hypothesis examples from different domains and will provide examples of failure cases for different methods across domains in the final version, which further strengthens their response.
However, the use of GPT-4o as the sole novelty evaluator in the LSR-Synth pipeline remains a concern. While the authors argue that consistently poor performance on LSR-Synth suggests the problems are indeed novel, relying solely on an LLM without external verification is still problematic, especially given ongoing research questioning LLMs’ ability to judge novelty or creativity.
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Reply to Comment 1.1.1:
Comment: Dear reviewer,
We appreciate your thoughtful review, and we are glad our rebuttal addressed most of your concerns. You raise a valid point about using GPT-4o as the sole novelty evaluator - this is indeed a limitation we acknowledge. Novelty assessment is genuinely challenging, and while LLM performance patterns suggest them to be helpful, independent verification would strengthen our claims. This is definitely a valuable direction for future work that would benefit from domain expert involvement. Thank you again for your constructive feedback throughout this process. | Summary: This paper introduces LLM-SRBench, a benchmark designed to evaluate LLMs on scientific equation discovery tasks. The authors identify a key problem: existing benchmarks like Feynman equations can be solved by LLMs through memorization rather than actual discovery. To address this, they develop two benchmark categories: (1) LSR-Transform, which transforms common equations into less familiar mathematical forms, and (2) LSR-Synth, which creates novel synthetic equations that combine known scientific terms with plausible synthetic components. The benchmark spans 239 challenging problems across chemistry, biology, physics, and material science domains. They show that state-of-the-art methods achieve only 31.5% symbolic accuracy, highlighting significant challenges in this field.
Claims And Evidence: The paper's main claims are well-supported by the evidence presented. The authors convincingly demonstrate the memorization issue through Figure 1, showing how performance on standard Feynman problems exhibits patterns consistent with memorization (sharp error drops and lower symbolic error rates) rather than actual reasoning and discovery. The experiments across multiple methods and LLM backbones provide strong evidence that their benchmark is substantially more challenging than existing ones. The performance analysis across different scientific domains, complexity levels, and generalization capabilities is thorough and supports their conclusions.
Methods And Evaluation Criteria: The methods for creating the benchmark are well-designed and appropriate. The LSR-Transform approach uses rigorous symbolic transformation while maintaining appropriate complexity and ensuring analytical solvability. The LSR-Synth methodology includes careful verification of both solvability (using numerical solvers) and scientific plausibility (through expert validation).
The evaluation metrics are comprehensive, including both numeric performance (accuracy to tolerance, NMSE) and symbolic accuracy. I particularly appreciate the validation of their GPT-4o-based symbolic evaluation against human experts (94.6% agreement), which strengthens confidence in their assessment approach. The inclusion of out-of-domain evaluation is also valuable for assessing true scientific understanding.
Theoretical Claims: N/A.
Experimental Designs Or Analyses: The experimental design is comprehensive and well-executed. The authors evaluate four different methods (Direct Prompting, SGA, LaSR, LLM-SR) using three different LLM backbones (Llama-3.1-8B-Instruct, GPT-4o-mini, GPT-3.5-turbo) with standardized conditions (1,000 LLM calls per problem).
I found the analyses of performance across equation complexity levels (Figure 4) and in-domain versus out-of-domain generalization (Figure 5) particularly informative. The correlation between symbolic accuracy and OOD performance (Figure 6) is an interesting finding that validates their evaluation approach.
However, it would be good to include more detailed case studies or error analyses to better understand which types of equations or mathematical patterns pose the greatest challenges for current methods.
Supplementary Material: Reviewed parts of the additional results.
Relation To Broader Scientific Literature: The paper effectively places itself within the broader literature on symbolic regression, scientific equation discovery, and LLM reasoning capabilities. It builds upon previous benchmarks (SRBench, SRSD) while addressing their limitations for LLM evaluation. The connection to literature on LLM reasoning fragility with unfamiliar representations (Mirzadeh et al., 2024; Xie et al., 2024) provides solid theoretical grounding for their approach.
Essential References Not Discussed: None that I'm aware of.
Other Strengths And Weaknesses: Strengths:
- The benchmark addresses a gap in evaluating LLMs on scientific discovery vs. memorization
- The evaluation across multiple methods, backbones, and domains is thorough
- The correlation between symbolic accuracy and OOD performance is an interesting finding
- The examples of output hypotheses in Figure 14 provide good qualitative insights
Weaknesses:
- While showing that current methods struggle, there's limited analysis of why they fail or which specific reasoning capabilities are lacking
- The synthetic problems, while validated for plausibility, may not perfectly capture real scientific discovery challenges
- Could benefit from more discussion of how its findings might influence future LLM designs to improve scientific reasoning
- Would be nice to see more discussion around if some of the equation transformations in LSR-Transform, while mathematically valid, are meaningful from a scientific perspective
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Have you identified specific patterns or characteristics in the equations where current methods consistently fail?
2. How sensitive is performance on your benchmark to the quality or quantity of provided data? In real scientific scenarios, data is often limited or noisy - have you explored this dimension?
3. The correlation between symbolic accuracy and OOD performance is intriguing. Does this relationship hold equally across all scientific domains, or are there areas where symbolic understanding is less predictive of generalization?
4. Your benchmark focuses on discovering equations given data and context. Have you considered extending it to evaluate LLMs' abilities to generate plausible hypotheses before seeing complete datasets, which is another important aspect of scientific discovery?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for dedicating your time and expertise to review our submission. Please find our responses below.
> * However, it would be good to include more detailed case studies or error analyses to better understand which types of equations or mathematical patterns pose the greatest challenges for current methods.
> * While showing that current methods struggle, there's limited analysis of why they fail or which specific reasoning capabilities are lacking
Thank you for the thoughtful suggestion. We examined the failure cases during rebutal period and noticed that LLM-based models usually don't fail due to the syntax function errors (such as missing variables or dependencies). Instead, most errors come from incorrect terms or combination of terms within the equations, reflecting mistakes due to semantic aspects of discovery for a given scientific problem. We could not identify a uniform pattern of specific mathematical relations that consistently challenge current discovery methods. We believe this is because LLM-based equation discovery involves a complex interplay of domain knowledge, search capabilities with data-driven feedback, and mathematical manipulation skills. To thoroughly study failure case patterns would require investigating all these dimensions. We agree with the reviewer on the importance of this research direction and consider it a promising avenue for future work.
> The correlation between symbolic accuracy and OOD performance is intriguing. Does this relationship hold equally across all scientific domains, or are there areas where symbolic understanding is less predictive of generalization?
Thank you for this thoughtful question. We have actually explored the correlation between symbolic accuracy and OOD performance across different domains (detailed in Figure 13 Appendix). Our results demonstrate that this positive correlation holds across all four domains. Symbolic understanding appears to be a reliable predictor of generalization capability in equation discovery.
> How sensitive is performance on your benchmark to the quality or quantity of provided data? In real scientific scenarios, data is often limited or noisy - have you explored this dimension?
We have not yet explored the impact of noise or data limitations in our current benchmark generation process. Our primary motivation was to develop a benchmark that helps the community build better general LLM-based equation discovery agents for scientific domains, addressing limitations in existing benchmarks for emerging LLM-based techniques. We fully agree with the reviewer on the significance of noise and limited data in real-world scientific discovery scenarios. This is one of the directions we're considering for future benchmark enhancements.
> Your benchmark focuses on discovering equations given data and context. Have you considered extending it to evaluate LLMs' abilities to generate plausible hypotheses before seeing complete datasets, which is another important aspect of scientific discovery?
We would like to clarify that our benchmark evaluates SOTA methods that already incorporate a two-phase approach: hypothesis generation followed by data-driven validation. In the first phase, LLMs generate plausible equation hypotheses without seeing the data, which are then refined based on how well they fit the data. We agree that evaluating pure hypothesis generation capabilities is an important dimension of scientific discovery. While our present focus has been on end-to-end data-driven scientific equation discovery, extending the benchmark to explicitly measure hypothesis quality before the data validation is also a valuable direction for future work. We also think that combining mathematical derivation processes with data-driven reasoning represents an interesting avenue for future research that has not yet been thoroughly explored in current methods.
> The examples of output hypotheses in Figure 14 provide good qualitative insights
As some reviewers have higlighted this example helpful, we plan to include more hypothesis examples from different domains in the revision of paper.
> * Could benefit from more discussion of how its findings might influence future LLM designs to improve scientific reasoning
> * Would be nice to see more discussion around if some of the equation transformations in LSR-Transform, while mathematically valid, are meaningful from a scientific perspective
Thank you for the suggestion. We will make sure to add more discussion regarding these points in the camera-ready version. | Summary: This paper introduces LLM-SRBench, a benchmark designed to evaluate Large Language Models' capabilities in scientific equation discovery. The authors address a limitation in existing benchmarks: they primarily consist of well-known equations from textbooks that LLMs may have memorized during training, potentially leading to performance metrics that reflect recitation rather than discovery abilities.
LLM-SRBench comprises 239 problems across two categories:
LSR-Transform (111 problems): Transforms Feynman physics equations into alternative mathematical forms by changing which variable is solved for, challenging LLMs to discover less familiar representations of known physical relationships.
LSR-Synth (128 problems): Creates problems across chemistry, biology, physics, and material science by combining established scientific terms with synthetic terms, requiring models to employ both scientific reasoning and data-driven discovery.
The authors evaluate several LLM-based equation discovery methods (Direct Prompting, SGA, LaSR, LLM-SR) using various LLM backbones (Llama-3.1-8B, GPT-3.5-turbo, GPT-4o-mini). Their findings show that the best-performing method achieves 31.5% symbolic accuracy, indicating challenges in scientific equation discovery.
The paper also presents an evaluation methodology that considers both data fidelity (numeric accuracy) and symbolic correctness, including an LLM-based approach for assessing mathematical equivalence across different representations. The authors note a correlation between symbolic accuracy and out-of-domain generalization.
This work provides a testbed for current methods and may contribute to advancing scientific equation discovery research.
Claims And Evidence: The paper convincingly asserts that LLM memorization is a factor in existing benchmarks, with memorization demonstrated through error curves; the authors leave open the possibility of alternative explanations. They further demonstrate the benchmark's difficulty with a convincing performance evaluation across methods and SOTA-standard LLMs.
Methods And Evaluation Criteria: The paper utilizes a two-pronged approach for dataset creation: transforming known equations through variable substitution and combining known scientific terms with synthetic elements. The benchmark spans four scientific domains with varying distribution of problems across domains. The evaluation employs dual metrics focusing on data fidelity (numeric accuracy/error) and symbolic accuracy, with separate assessments for in-domain and out-of-domain generalization. The authors introduce an LLM-based approach for evaluating symbolic equivalence, validated through comparison with human judgments. The paper evaluates various LLM-based scientific equation discovery methods but does not include non-LLM symbolic regression baselines for comparison. Questions remain about whether the synthetic problems authentically model scientific discovery processes rather than testing mathematical manipulation skills.
Theoretical Claims: This paper is empirical in nature. No significant theoretical claims are made.
Experimental Designs Or Analyses: The paper provides appropriately comprehensive coverage by standardizing methods to 1k LLM calls while preserving core algorithmic structures, evaluating multiple methods (Direct Prompting, SGA, LaSR, LLM-SR) across different LLM implementations. Their comparison of performance across equivalent complexity levels demonstrates that challenge stems from semantic transformation rather than structural complexity. The correlation analysis between symbolic accuracy and OOD performance validates their evaluation metrics. However, the design lacks ablation studies to isolate which components drive performance differences, and while domain performance variations are noted, there's no systematic exploration of whether different methods have domain-specific advantages.
Supplementary Material: The supplementary material provides clarifying examples about the nature of the dataset, providing the reader with a more wholistic intuition about the dataset without having to review a hosted repository.
Relation To Broader Scientific Literature: While I am not an expert in this field, the paper appears to effectively situate itself within several research domains, connecting to existing symbolic regression benchmarks while addressing their limitations for LLM evaluation
Essential References Not Discussed: I am not aware of any essential references that are not discussed.
Other Strengths And Weaknesses: This paper is very well written and seems to explain the nuances of the field well, deserving to be a part of the published record.
Other Comments Or Suggestions: None.
Questions For Authors: Do you have either intuition or insight into specific criteria for when numeric performance and symbolic accuracy metrics diverge?
The benchmark design assumes that transforming equations (LSR-Transform) and combining known with synthetic terms (LSR-Synth) effectively models scientific discovery. How do you justify that these approaches genuinely reflect how scientists discover new equations in practice, rather than simply creating mathematically challenging problems? Would performance on these tasks predict success in real scientific discovery?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for dedicating your time and expertise to review our submission. Please find our responses below.
> * there's no systematic exploration of whether different methods have domain-specific advantages.
We agree this is an important consideration, but it falls outside our study's scope. Our benchmark aims to help community towards building better general LLM-based equation discovery agents applicable across domains. Domain-specific variations mostly come from the LLM's knowledge rather than the agentic discovery framework itself. Further experiments with different LLM backbones would be helpful to study this question in more depth.
> Do you have either intuition or insight into specific criteria for when numeric performance and symbolic accuracy metrics diverge?
Thank you for the thoughtful question. This is indeed a common challenge in equation discovery. Equations with good numeric accuracy may differ significantly in symbolic manner. Conversely, equations with similar symbolic structures can also exhibit significantly different numeric behaviors due to constant/coefficient variations affecting function behavior. This is why our benchmark incorporates both numeric and symbolic metrics for comprehensive evaluation.
> The benchmark design assumes that transforming equations (LSR-Transform) and combining known with synthetic terms (LSR-Synth) effectively models scientific discovery. How do you justify that these approaches genuinely reflect how scientists discover new equations in practice, rather than simply creating mathematically challenging problems? Would performance on these tasks predict success in real scientific discovery?
Thanks for raising this important question. Whether performance on these tasks predicts success in real scientific discovery remains an open research question. But we think that our benchmark can be a good starting point to guide models towards that direction, particularly in the task of scientific equation discovery.
To ensure our benchmark reflects scientific discovery rather than just creating mathematically challenging problems, we implemented filtering steps in the design of benchmark (detailed in Section 2, Figures 4, 8, and 10) to avoid lengthy problems with excessive mathematical and syntax complexity. | null | null | null | null | null | null |
Linear Transformers as VAR Models: Aligning Autoregressive Attention Mechanisms with Autoregressive Forecasting | Accept (poster) | Summary: The paper addresses time series forecasting by aligning linear-attention Transformer with vector autoregressive (VAR). The authors reveal that while single-layer linear attention mechanisms naturally exhibit a dynamic VAR structure, but multi-layer Transformers can misalign with the autoregressive forecasting objective. To address this, they propose a linear-attention Transformer variant that incorporates dynamic VAR weights by reorganizing input-output flows. Empirical results show the proposed models improve the performance and interpretability compared to several baseline models.
Claims And Evidence: The claims made in the paper are generally supported, for example, the authors provide a theoretical analysis of how linear attention can be interpreted as a VAR model. However, some claims are made based on empirical results from previous works. They claim that "linear attention can outperform vanilla attention in time series forecasting tasks". This may not be the consensus in the field. It is also inconsistent with the evaluations (Table 1), where linear-attention Transformer can not generally outperform the vanilla ones. Some claims may be oversimplified: "Replacing $\sigma$ with an identity simplifies it to linear attention," Which linear attention is referred to? This assumption makes the Attn() a linear transformation of X. Some claims can be biased: "Transformers are effective for modeling complex sequence relationships (e.g., in NLP), their architecture conflicts with VAR’s goal of explicitly representing lag-based dependencies." The author does not provide evidence that explicit VAR can help in terms of training models for time series rather than natural language. Therefore, it is better to explain the "capability of modeling complex sequence relationships" and why the alignment with explicit VAR is important.
Methods And Evaluation Criteria: The authors use standard benchmark datasets for time series forecasting, such as Weather, Solar, and ETT, which are widely adopted in the previous works.
Theoretical Claims: The proof in Section 3 appears to be correct, but there are some incorrect assumptions: (1) Section 2.2: Equation (1) omits the scaling factor, (2) The recurrent form of Attention relies on the causal mask. However, I am not certain about the proposed architecture adopting the causal mask. It seems that Transformers in Table 1 are not decoder-only ones? Please correct me if I'm mistaken..
Experimental Designs Or Analyses: * I recommend the author to evaluate more baseline models, including more counterpart linear-attention Transformers (currently 2), and decoder-only Transformers (currently 0).
* How about the performance when using more Transformer layers? Is the training process of SAMoVAR stable?
Supplementary Material: I have read the results in the supplementary material.
Relation To Broader Scientific Literature: This paper focuses on refining Transformers for time series forecasting.
Essential References Not Discussed: The paper can benefit from discussing more recent advancements in autoregressive Transformers for time series forecasting, such as TimesFM [ICML 2024]. Whether the method proposed in this paper can improve the performance on similar models?
Other Strengths And Weaknesses: * Strength: The paper presents a theoretically proof to reveal the similarity between simplified linear Transformers with VAR models.
* Weakness: The motivations of aligning linear Transformer with VAR are not well supported. To my best knowledge, linear Transformers are not the dominant choice in time series forecasting.
Other Comments Or Suggestions: See Above.
Questions For Authors: Is there information leakage when the above method is used for training encoder-only models? Although the model is autoregressive supervised by the groundtruth in multi-step prediction, there is no groundtruth at each step during inference.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >Linear attention outperform ... may not be the consensus
>Linear Transformers are not the dominant ...
Thank you for the question. Our claim is based on [1] (https://arxiv.org/abs/2410.03159, cited at line 479), which suggests AR linear attention may outperform vanilla attention in TSF. We also support this by referencing linear attention's performance in other position-sensitive domains.
We will revise the text to include qualifiers (e.g., sometimes) for clarity. Additionally, we provide more results at [Link (Table 1)](https://anonymous.4open.science/r/SAMoVAR-Rebuttal-F83C) comparing linear and softmax attention, showing advantage.
Prior works (DLinear, PatchTST ...) have noted overfitting in TSF Transformers. Softmax attention’s strong expressiveness can overfit noise. In contrast, linear attention, due to the linearity of query, key, and value, retains an AR form [1] and also introduces a dynamic VAR structure:
AR form of attention [1]:
$$
\mathbf{o}\_t = \sum\_{i=1}^t \mathbf{w}\_{t,i} \mathbf{v}\_i \ , \mathbf{w}\_{t,i} = \mathbf{q}\_t \mathbf{k}\_i^\top \in \mathbb{R}^d
$$
VAR form of linear attention [This paper]:
$$
\mathbf{o}\_t = \sum_{i=1}^t \mathbf{k}\_i \mathbf{A}\_{t,i} \ , \mathbf{A}\_{t,i} = \mathbf{q}\_t^\top \mathbf{v}\_i \in \mathbb{R}^{d \times d}
$$
This allows for dual linear interpretability, with stronger regularization, better suited for channel- and token-wise linear mixing at each layer, suited for TSF data commonly modeled with AR/VAR structures.
>Inconsistent with (Table 1) ...
This aligns with Table 1: LinTrans outperforms softmax-based models (iTransformer, PatchTST, EncFormer). The only exception is CATS, which is MLP-based and does not use softmax attention.
>Some claims may be oversimplified: Replacing $\sigma$ ...
Apologies—this should read “simplified to linear attention with a linear kernel.” This is a standard baseline in recent works like Gated Linear Attention and RetNet. We’ll clarify this in the revision.
>Evidence that explicit VAR ... "capability of modeling complex ..."
Due to space limits, please refer to our response to Reviewer RLuA for discussion on NLP data.
> Incorrect assumptions: (1) ..., (2) ...
(1) Apologies—we’ll clarify this. The scaling factor acts like a softmax temperature and doesn’t affect analysis.
(2) Yes, all attention structures in our methodology use decoder-only attention with a causal mask. A comparison is provided below:
Encoder-only (without causal mask):
$$
\mathbf{O} = \mathbf{Q} \mathbf{K}^\top \mathbf{V} \\
\mathbf{o}\_t = \mathbf{q}\_t \sum_{i=1}^N \mathbf{k}\_i^\top \mathbf{v}\_i
$$
Decoder-only (with causal mask, used in this paper):
$$
\mathbf{O} = \mathbf{M} \odot (\mathbf{Q} \mathbf{K}^\top) \mathbf{V} \\
\mathbf{o}\_t = \mathbf{q}\_t \sum\_{i=1}^t \mathbf{k}\_i^\top \mathbf{v}\_i
$$
Timesteps are $\{1, ..., t, ..., N\}$. For encoder-only, $\mathbf{q}_t$ sees all tokens; for decoder-only, it sees only up to step $t$. This notation is standard in linear attention literature.
>Evaluate more baseline
Note that LinTrans uses decoder-only attention, while iTransformer, PatchTST, and EncFormer use encoder-only softmax attention. Additional results at [Link (Table 1)](https://anonymous.4open.science/r/SAMoVAR-Rebuttal-F83C) compare with AR softmax and gated linear attention.
>Performance ... more layers
Table 2 shows that ~3 layers of SAMoVAR work well across most datasets, with other choices showing no major drop in performance. The $l$-th layer output aggregates results from $n^{\text{path}}_{t,j,l}$ paths per key observation:
$$
\mathbf{o}\_t^{(l)} = \sum\_{\text{All Paths}} \mathbf{P}\_{t,j,\{i\_1, \cdots, i\_{l-1}\}}^{(l)} \mathbf{k}\_i^{(1)\top} = \sum\_{\text{All Paths}} \mathbf{v}\_{i\_1}^{(l)\top} [\mathbf{q}\_t^{(l)} \,\mathbf{v}\_{i\_2}^{(l-1)\top} \mathbf{q}\_{i\_1}^{(l-1)} \;\cdots\; \mathbf{v}\_{j}^{(1)\top}] \mathbf{q}\_{i_{l-1}}^{(1)} \mathbf{k}\_i^{(1)\top}
$$
Each path is scaled by the bracketed scalar. Normalizing q and k keeps inner products close to <1, avoiding instability. The only risk of deeper models comes from the increase in path count ($n^{\text{path}}_{t,j,l}$), which may cause overfitting of too many dynamics for longer lags.
>More recent advancements ... TimesFM ...
We will add a Related Works section for recent TSF advances to support the use of AR Lin Attn in TSF.
>Is there information leakage...
Our AR/ARX tokenization adds an AR loss between non-overlapping PatchTST tokens. Each token covers the full horizon $L_P$, allowing us to follow the same training/testing setup as prior works, with only one added loss term. The decoder-only enables effective training, functionally similar to shorter-context data augmentation or varying-context multitask training.
This allows us to integrate AR attention without changing the experimental setup. Like previous works, we use one-step prediction covering $L_P$, avoiding iterative prediction and any risk of data leakage.
---
Rebuttal Comment 1.1:
Comment: Thanks for the detailed rebuttal. I have raised the score as the authors have resolved most of the concerns. | Summary: This paper addresses the misalignment between deep Transformer architectures and autoregressive objectives in time series forecasting (TSF), proposing Structural Aligned Mixture of VAR (SAMoVAR) to integrate interpretable dynamic VAR weights into multi-layer linear Transformers. By reorganizing the input-output flow and aligning the structure with VAR models, SAMoVAR enhances the ability to capture data generative processes, achieving improved performance, interpretability, and efficiency compared to state-of-the-art TSF models through experiments on synthetic and real-world datasets.
## update after rebuttal
I have reviewed your responses and those to other reviewers. While some concerns have been addressed, I remain unconvinced regarding the theoretical insights or experimental results on capturing periodicity and non-linear patterns. Therefore, I will maintain my original score.
Claims And Evidence: The assertion that single-layer linear attention aligns with a dynamic VAR structure is backed by rigorous theoretical derivations (Equations 2–3) and validated through synthetic experiments (Figures 3–4). Additionally, the improved performance of SAMoVAR over baseline models is demonstrated across multiple datasets, with significant reductions in MSE (e.g., 30% on the Solar dataset compared to previous models), providing strong empirical support for the effectiveness of the proposed model.
However, the claim that SAMoVAR provides interpretable dynamic VAR weights could be further strengthened. While visualizations (e.g., Figure 5) illustrate the temporal influence paths, they lack quantitative analysis.
Methods And Evaluation Criteria: The paper introduces "Robust Path Pruning" to ensure numerical stability and control weight variance in SAMoVAR. While the ablation studies show that removing RMSNorm degrades performance, further validation is needed to fully support the claims around path pruning. Specifically, the paper lacks detailed metrics on the percentage of paths pruned and the correlation between pruned paths and model performance. Additionally, theoretical analysis on the probability of query-value orthogonality and comparison to active pruning methods would strengthen the claims. Assessing the impact of pruning on the model’s ability to capture long-term dependencies and measuring the rank of the resulting weight matrices would also provide deeper insights into the effectiveness of the pruning mechanism.
Theoretical Claims: Multi-Layer Alignment: The claim that "multi-layer linear attention aligns with VAR" (Sec. 4.1) relies on recursive expansions (Eq. 5) but lacks formal proof. For instance, it is unclear whether the cumulative paths preserve VAR properties (e.g., stationarity).
Stability Guarantees: No theoretical analysis ensures that path pruning or RMSNorm prevents gradient explosion in deep layers.
Experimental Designs Or Analyses: Batch size adjustments for large datasets (e.g., PEMS07 excluded due to batch size=1) may introduce bias. No sensitivity analysis is provided.
Supplementary Material: The supplementary material includes implementation details and additional visualizations. However:
- No proof of multi-layer VAR alignment is provided.
- The synthetic task’s ground-truth VAR parameters (Sec. 5.1) are not described, limiting reproducibility.
Relation To Broader Scientific Literature: The work bridges classical VAR models and modern linear Transformers, extending prior efforts like [Katharopoulos et al. 2020] (linear attention as RNNs) and [Zeng et al. 2023] (Transformer-VAR comparisons).
Essential References Not Discussed: Limited discussion of concurrent work on efficient attention mechanisms (e.g., Retentive Networks [Sun et al. 2023], H3 [Dao et al. 2023]), which also achieve linear complexity.
Other Strengths And Weaknesses: Strengths:
- Originality: The integration of VAR theory into linear attention is novel, offering a fresh perspective on Transformer interpretability.
- Significance: The method’s efficiency and performance improvements are practically valuable for real-world TSF applications.
Weaknesses:
- Clarity: The temporal influence path concept (Sec. 4.1) is overly abstract. A step-by-step example (e.g., for 2-layer SAMoVAR) would improve readability.
Other Comments Or Suggestions: The current model framework diagram is insufficient for fully understanding the proposed mechanisms, especially the Temporal Influence Path and Robust Path Pruning. Enhancing the visual representation with more detailed diagrams or flowcharts would significantly aid in clarifying these complex components and their integration into the overall architecture.
Questions For Authors: 1.Time series often exhibit periodic and non-linear patterns, especially in long-term forecasting. How does SAMoVAR effectively capture these characteristics, and are there theoretical insights or experiments demonstrating its ability to handle periodicity and non-linear interactions?
2.Irregular time series data are common in healthcare applications. Can the authors discuss SAMoVAR’s potential advantages in handling such data, particularly in medical forecasting tasks?
3.The paper claims that SAMoVAR maintains O(N) complexity, but the new architecture might introduce additional overhead. Can the authors provide a detailed complexity analysis, especially for the Temporal Influence Path mechanism?
4.The experiments show SAMoVAR’s effectiveness with specific hyperparameters. How robust are these settings across different datasets, and can the authors provide guidelines for selecting optimal configurations in various scenarios?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >No theoretical analysis for robust path pruning
Thank you for the insightful question. We provide a proof sketch below.
**Theorem 1**: RMSNorm applied to query and value vectors bounds the magnitudes of dot products in temporal influence paths, preventing numerical instability.
**Proof Sketch**:
Query and value vectors are normalized using RMSNorm:
$$\mathbf{q}_t^{(l)} = \text{RMSNorm}(\mathbf{x}_t^{(1)}\mathbf{W}_q^{(l)}), \quad \mathbf{v}_i^{(l)} = \text{RMSNorm}(\mathbf{x}_i^{(1)}\mathbf{W}_v^{(l)})$$
where:
$$\text{RMSNorm}(\mathbf{y}) = \frac{\mathbf{y}}{\sqrt{\frac{1}{d}\sum_{j=1}^{d} y_j^2}} \odot \mathbf{g}$$
This bounds their dot product:
$$|\mathbf{v}\_{i}^{(l)\top} \mathbf{q}\_{t}^{(l)}| \leq \|\mathbf{g}\_v^{(l)}\|_2 \cdot \|\mathbf{g}\_q^{(l)}\|_2 \approx 1$$
with proper initialization of small gain parameters $\mathbf{g}$ (e.g., $\sim \mathcal{N}(0,\frac{1}{d})$).
For a temporal influence path with $l$ layers:
$$|\mathbf{P}\_{t,j,\{i_1,...,i\_{l-1}\}}^{(l)}| = |\mathbf{v}\_{i_1}^{(l)\top} \mathbf{q}\_t^{(l)}| \cdot ... \cdot |\mathbf{v}\_{j}^{(1)\top} \mathbf{q}\_{i\_{l-1}}^{(1)}| \leq 1$$
In practice, path magnitudes decrease with depth as dot products are typically smaller than 1.
**Theorem 2**: As dimension $d$ increases, random vectors become increasingly orthogonal, naturally pruning unnecessary paths.
**Proof Sketch**:
For normalized vectors $\hat{\mathbf{q}}$ and $\hat{\mathbf{v}}$ with random initialization, their dot product:
$$\hat{\mathbf{q}}^T \hat{\mathbf{v}} = \sum_{i=1}^d \hat{q}\_i \hat{v}\_i$$
has mean 0 and variance $\frac{1}{d}$. By the Central Limit Theorem, for large $d$, this approaches $\mathcal{N}(0,\frac{1}{d})$.
For threshold $\epsilon > 0$, the probability of near-orthogonality is:
$$P(|\hat{\mathbf{q}}^T \hat{\mathbf{v}}| < \epsilon) \approx 2\Phi\left(\epsilon\sqrt{d}\right) - 1$$
which approaches 1 as $d$ increases.
For a path:
$$\mathbf{P}\_{t,j,\{i_1,...,i\_{l-1}\}}^{(l)} = \mathbf{v}\_{i\_1}^{(l)\top} \mathbf{q}\_t^{(l)} \cdot ... \cdot \mathbf{v}\_{j}^{(1)\top} \mathbf{q}\_{i_{l-1}}^{(1)}$$
With larger $d$, the likelihood of a near-zero dot product increases, pruning irrelevant paths while training strengthens important ones.
>The claim that SAMoVAR provides interpretable ... could be further strengthened.
Our current temporal influence path visualization offers interpretability similar to attention maps but does not yet match that of traditional MLE-based VAR models. This paper focuses on SAMoVAR’s predictive performance, though full statistical interpretability is possible through:
1. Initializing query/value weights via SVD of training set covariance.
2. Breaking symmetry by fixing an element in the q/v weight matrices.
3. Removing MLPs, pre-normalization, patching, and projections for full linearity.
4. Training with MLE loss.
5. Estimating parameter uncertainty using asymptotic covariance for standard errors.
6. Applying the Delta method to propagate uncertainty in dynamic VAR weights.
These changes would enable full interpretability but reduce model flexibility and accuracy. We’re happy to share our ongoing works in this direction, though it is beyond this paper’s current scope.
>Whether the cumulative paths preserve VAR properties (e.g., stationarity)
>Proof of VAR structure
SAMoVAR is not constrained to classic stationarity. Enforcing eigenvalues within the unit circle, especially with long lags, would limit expressiveness and harm predictive power. As for the structural derivation of the model, Please see the proof in our response to Reviewer aK3c. Thank you!
>Batch size adjustments may introduce bias.
As noted in Appendix (line 707), we use gradient accumulation to maintain an effective batch size of 32 when reducing batch size. A reference will be added in the revision.
>Ground-truth VAR parameters (Sec. 5.1) are not described, limiting reproducibility.
The VAR parameters are shown in the top-left heatmap of Figure 3. All experiments and code from Section 5.1 are available in `visualization/model_visualize.ipynb` to ensure maximized reproducibility.
>non-linear patterns ... ability to handle periodicity and non-linear interactions...
Due to space limits, please refer to our response to **Reviewer RLuA** for discussion on NLP and complex data.
>SAMoVAR... in medical forecasting tasks
We use standard TSF benchmarks, which contain irregular patterns in some data (like Weather, ETTh1, ETTh2). SAMoVAR performs well, suggesting potential for irregular medical data.
>Proof of SAMoVAR maintains O(N) complexity
Due to space limits, please see the **proof** in our response to **Reviewer ZzwP**.
>guidelines for selecting optimal configurations
We use fixed hyperparameters across all datasets. The fixed $L_I$ settings highlight robustness compared to baselines needing $L_I$ tuning. See our response to Reviewer ZzwP, and Appendix A.3, where full configuration are ready to use without any modification. | Summary: This paper demonstrates that a single linear attention layer behaves like a dynamic VAR model and that deeper Transformers can be restructured to align with autoregressive objectives. Based on these insights, the authors introduce SAMoVAR, a Transformer variant that leverages dynamic VAR weights to enhance forecasting performance, interpretability, and efficiency.
Update after rebuttal: Thanks for the detailed rebuttal. I appreciate the authors' efforts in addressing my concerns and helping me better understand the work. Therefore, I will maintain my original rating.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: N/A.
Experimental Designs Or Analyses: Yes.
Supplementary Material: N/A.
Relation To Broader Scientific Literature: The authors introduce SAMoVAR, a Transformer variant that leverages dynamic VAR weights to enhance forecasting performance, interpretability, and efficiency.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: I am not very familiar with the time series forecasting task, but the paper reads logically and intuitively.
Strengths:
1. The motivation behind the proposal of SAMoVAR is well-founded.
2. The theoretical explanations are comprehensive and clear.
3. The experiments and the analysis of experimental results are thorough and convincing.
Question:
Why does the validation loss in Figure 4 exhibit significant oscillations during the training process?
Minor Issue:
Line 18: The paper refers to VAR before defining it.
Other Comments Or Suggestions: See strengths and weaknesses.
Questions For Authors: See strengths and weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >Why does the validation loss in Figure 4 exhibit significant oscillations during the training process?
Thank you very much for taking the time to read our paper and for acknowledging its contributions.
We apologize for the misunderstanding. In Figure 4, we cropped the Y-axis of the validation loss curve. Like the training loss, it starts around 0.1 and decreases over epochs. However, using 0.1 as the upper bound would make the convergence of all three curves indistinguishable in this compact figure. As shown, the validation loss fluctuates within ±0.002 in later epochs, consistent with the training loss scale.
Notably, SAMoVAR surpasses the final performance of the other two baselines after just 30 epochs. The Y-axis scaling was chosen purely to highlight this advantage for clarity.
You can verify more of this in our code repository: see `visualization/model_visualize.ipynb`, specifically `In [5]` and `Out [5]`, where we use `plt.ylim(-0.01, 0.1)` for the training loss and `plt.ylim(0.0025, 0.0085)` for the validation loss.
>Line 18: The paper refers to VAR before defining it.
Thank you for pointing this out. We will ensure that VAR is properly defined upon its first appearance in the revision.
>Theoretical Claims:
>N/A.
Thank you for your positive feedback. Even though you didn’t explicitly request it, we’re happy to provide a more detailed derivation of how SAMoVAR’s multi-layer linear attention can be expressed as a VAR structure, to further support your understanding. If you're already familiar with this, feel free to skip the following explanation. Thank you again!
**Proposition** For any $l \geq 1$, the output $\mathbf{o}_t^{(l)}$ can be expressed as VAR structure:
$$\mathbf{o}\_t^{(l)\top} = \sum\_{j=1}^t \mathbf{B}\_{t,j}^{(l)} \mathbf{x}\_j^{(1)\top}$$
**Proof by Induction:**
**Base Case (l=1)** For a single linear attention layer, we have:
$$\mathbf{o}\_t^{(1)\top} = \sum_{i=1}^t \mathbf{A}\_{t,i}^{(1)} \mathbf{k}\_i^{(1)\top} = \sum\_{i=1}^t \mathbf{A}\_{t,i}^{(1)} \mathbf{x}\_i^{(1)\top}$$
Since $\mathbf{k}\_i^{(1)} = \mathbf{x}\_i^{(1)}$, we define $\mathbf{B}\_{t,i}^{(1)} = \mathbf{A}\_{t,i}^{(1)}$, which gives us the VAR form for the first layer.
**Inductive Step** The key insight is the relationship between outputs and inputs across layers. When we use $\mathbf{k}\_i^{(l+1)} = \mathbf{o}\_i^{(l)}$, we get:
$$\mathbf{o}\_t^{(l+1)\top} = \sum\_{i=1}^t \mathbf{A}\_{t,i}^{(l+1)} \mathbf{o}\_i^{(l)\top}$$
Substituting the inductive hypothesis and rearranging the sums:
$$\begin{aligned}
\mathbf{o}\_t^{(l+1)\top} &= \sum\_{i=1}^t \mathbf{A}\_{t,i}^{(l+1)} \left(\sum\_{j=1}^i \mathbf{B}\_{i,j}^{(l)} \mathbf{x}\_j^{(1)\top}\right) \\
&= \sum\_{j=1}^t \sum\_{i=j}^t \mathbf{A}\_{t,i}^{(l+1)} \mathbf{B}\_{i,j}^{(l)} \mathbf{x}\_j^{(1)\top} \\
&= \sum\_{j=1}^t \left(\sum_{i=j}^t \mathbf{A}\_{t,i}^{(l+1)} \mathbf{B}\_{i,j}^{(l)}\right) \mathbf{x}\_j^{(1)\top}
\end{aligned}$$
Therefore:
$$\mathbf{o}\_t^{(l+1)\top} = \sum\_{j=1}^t \mathbf{B}\_{t,j}^{(l+1)} \mathbf{x}\_j^{(1)\top}$$
Where:
$$\mathbf{B}\_{t,j}^{(l+1)} = \sum\_{i=j}^t \mathbf{A}\_{t,i}^{(l+1)} \mathbf{B}\_{i,j}^{(l)}$$
This recursive definition of $\mathbf{B}_{t,j}^{(l)}$ captures all possible influence paths from time $j$ to time $t$ through $l-1$ intermediate points, confirming that multi-layer linear attention maintains an VAR structure throughout the network. | Summary: This paper demonstrates that autoregressive linear attention can be interpreted as a rank-1 vector autoregressive (VAR) model. Building upon this perspective, the authors introduce SAMoVAR, a novel model achieved by stacking multiple linear attention layers. SAMoVAR overcomes the inherent rank-1 limitation of linear attention, thus enhancing the model's expressiveness and forecasting performance on time series tasks.
Claims And Evidence: The claims presented in the paper are supported by both theoretical analyses and empirical evidence.
Methods And Evaluation Criteria: The authors evaluate the proposed method across multiple multivariate time series forecasting datasets, demonstrating consistent improvements over state-of-the-art methods on most datasets.
Theoretical Claims: The theoretical derivations in the paper are clearly presented. I did not identify any major issues in the theoretical analysis.
Experimental Designs Or Analyses: The main comparative experiments are well-designed. However, the explainability section lacks clarity. This aspect needs further clarification (see Questions for Authors).
Supplementary Material: I have reviewed the appendix.
Relation To Broader Scientific Literature: The paper provides a novel perspective by framing linear attention in the VAR context, potentially bridging VAR models and linear attention architectures. However, connections to the linear attention literature could be strengthened further, particularly by directly comparing SAMoVAR with Linear Attention and its variants. Such comparisons could enhance accessibility for audiences from the Linear Transformer and LLM communities.
Essential References Not Discussed: The references are sufficiently comprehensive. However, integrating more explicit discussions about linear attention approaches prevalent in the broader literature (e.g., https://arxiv.org/pdf/2210.10340; https://arxiv.org/pdf/2006.16236; https://arxiv.org/pdf/2405.13956) would strengthen connections to related work.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: Formatting / Typos:
1. The page header is still shown as "Submission and Formatting Instructions for ICML 2025".
Questions For Authors: [Q1] Could you provide insight into how your VAR framework addresses or mitigates common issues with linear attention and its variants, such as attention dilution and unbounded gradients described by Qin et al. (https://arxiv.org/pdf/2210.10340)?
Under the VAR interpretation, what specifically causes these issues in linear attention and its variants?
Which of these known problems does SAMoVAR solve or alleviate, and which problems persist? Please clarify the underlying reasons.
[Q2] The current explainability analyses primarily highlight smoother temporal weights and locality. Could you further clarify how SAMoVAR's VAR structure explicitly enhances interpretability regarding task-specific insights?
[Q3] Have you evaluated SAMoVAR in language modeling tasks? If yes, how does its performance compare with traditional linear attention methods?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >However, integrating more explicit discussions about linear attention...
Thank you for the valuable suggestion. Currently, related literature is only discussed in the Introduction and Background. We will add a Related Work section in the revision for a more thorough and structured discussion.
>The page header is still shown as "Submission and Formatting Instructions for ICML 2025".
Thank you for pointing this out. We will ensure the correct header format is used in the revision to comply with the guidelines.
>Could you provide insight into how your VAR framework addresses or mitigates common issues with linear attention and its variants
Thank you for the insightful question. Prior work addresses the unbounded gradient issue by normalizing $ \mathbf{o}_t $. Similarly, in SAMoVAR, we apply RMSNorm to stabilize computations:
$$
\phi(\mathbf{q}_t)^{(l)} = \text{RMSNorm}(\mathbf{x}_t^{(1)} \mathbf{W}_q^{(l)}),
\quad \phi(\mathbf{k}_i)^{(1)} = \mathbf{x}_i^{(1)},
\quad \phi(\mathbf{k}_i)^{(l)} = \mathbf{o}_i^{(l-1)},
\quad \mathbf{v}_i^{(l)} = \text{RMSNorm}(\mathbf{x}_i^{(1)} \mathbf{W}_v^{(l)})
$$
Note that $ \mathbf{x}_i^{(1)} $ is also normalized beforehand. This aligns well with the approach used in the referenced work.
The notion of *attention dilution* suggests that softmax attention tends to focus on local token relationships. However, we caution against a potential causality issue here: in NLP, softmax attention appears to model local relationships not because of an inherent bias, but because NLP data often demands such modeling. Thanks to its strong selectivity, softmax attention can naturally focus on local context even without explicit inductive bias: unlike linear attention, which tends to produce more diffuse attention patterns due to weaker selectivity. In contrast, for time series data, softmax attention, being a smooth approximation of the max operation, can overly concentrate on specific intervals. Yet time series typically exhibit stable temporal patterns such as lagged autocorrelations, cycles, seasonality, and trends. These effects are less variable than token-wise dependencies in NLP. Therefore, a VAR-based inductive bias is better suited to capture these temporal consistent structures, avoiding the overly sharp, localized focus induced by softmax attention, which may result in overfitting as stated in previous Transformer-based TSF works.
>The current explainability analyses primarily highlight smoother temporal weights and locality. Could you further clarify how SAMoVAR's VAR structure explicitly enhances interpretability regarding task-specific insights?
Thank you for the question. As noted earlier, attention in NLP rarely models effects tied to absolute lag positions, since the context relationships vary greatly across inputs. This differs significantly from the stable, linearizable lag patterns seen in autocorrelated VAR processes.
In contrast, tasks involving time series, images, speech, and those in Long Range Arena (https://arxiv.org/abs/2011.04006) are more position-sensitive. Recent studies on efficient linear attention often evaluate on these domains. While many linear attention variants struggle to outperform vanilla Transformers on NLP tasks, they often surpass them on position-related tasks, especially LRA benchmarks.
Our interpretation of linear attention as a form of VAR modeling helps explain this: VAR weights can explicitly capture stable positional patterns, such as autocorrelations in token space, offering a better inductive bias in these settings with consistent positional patterns.
>Have you evaluated SAMoVAR in language modeling tasks? If yes, how does its performance compare with traditional linear attention methods?
Thank you for the valuable question. Building on the previous responses, you may understand that our positioning of SAMoVAR is as follows: it is particularly suited for data with clear autoregressive structure, strong autocorrelations, and stable positional effects, as seen in TSF data.
For NLP tasks, SAMoVAR’s dynamic weight matrix would need to vary more significantly, similar to softmax, to adapt to diverse input patterns. This remains an interesting direction for future exploration. | Summary: This paper proposes structural modifications to linear Transformer architectures to better align them with the Vector Autoregressive (VAR) framework, which is widely used in time series forecasting. The authors show that while a single-layer linear attention module can naturally express a dynamic VAR structure, standard multi-layer Transformer designs introduce misalignments that hinder interpretability and forecasting performance. To address this, they introduce SAMoVAR (Structural Aligned Mixture of VAR), a novel Transformer variant that reorganizes the attention and MLP layers to preserve a coherent dynamic VAR interpretation across multiple layers. The paper presents both theoretical formulations and empirical evaluations, demonstrating that SAMoVAR achieves improved accuracy, interpretability, and computational efficiency on a range of standard multivariate time series forecasting benchmarks, outperforming existing state-of-the-art models.
Claims And Evidence: The primary claim of the paper is that the proposed SAMoVAR architecture improves over state-of-the-art Transformer-based models for time series forecasting in terms of accuracy, interpretability, and computational efficiency. This claim is generally supported by empirical evidence: the authors report strong performance across a wide range of standard benchmarks, and the improvements in accuracy are consistent across datasets.
However, some concerns remain. First, while the reported results show SAMoVAR outperforming prior methods, the performance margins differ from those presented in original papers of some recent baselines, suggesting that the experimental setup may not fully match those prior works. Clarification on baseline implementations and training details would help validate the comparison.
Second, the claim of superior computational efficiency is less clearly supported. Table 8, which is meant to demonstrate SAMoVAR's efficiency, includes results that appear counterintuitive or internally inconsistent. These discrepancies warrant further clarification from the authors to substantiate the efficiency claim.
Methods And Evaluation Criteria: The proposed method and evaluation criteria are appropriate for the time series forecasting task. The paper follows standard practices in the field, employing widely-used multivariate TSF benchmark datasets and comparing against strong Transformer-based baselines. The experimental setup, including input/output lengths and tokenization strategies, is consistent with prior work, ensuring a fair and relevant evaluation of the proposed model.
Theoretical Claims: The paper does not include formal theoretical claims or proofs. While it provides intuitive interpretations and derivations connecting linear attention mechanisms to dynamic VAR structures, these are presented in an informal manner without rigorous theoretical guarantees. This absence raises some concern regarding whether the observed performance gains stem from fundamental modeling improvements or from design choices that may implicitly favor the proposed method. Including formal analysis or clearer theoretical justification would strengthen the paper’s contribution.
Experimental Designs Or Analyses: The experimental design and analysis in the paper are generally sound. The authors evaluate the proposed method across a diverse set of standard time series forecasting benchmarks and compare against strong, commonly used baselines. However, there are two notable concerns. First, the reported results for some prior state-of-the-art methods differ from those presented in their original papers, raising questions about reproducibility and consistency in implementation. Second, the compute efficiency claims—particularly those in Table 8—are not fully convincing and appear inconsistent or counterintuitive. These aspects would benefit from further clarification and verification.
Supplementary Material: The reviewer went through all of the supplementary material. While it provides additional visualizations and implementation details, there are still concerns regarding the results in Table 8. Specifically, the reported compute efficiency figures appear questionable and are not fully aligned with expectations based on the main model structure. Additionally, some of the figures illustrating temporal influence paths lack clarity or consistency with the main text, making it difficult to fully interpret or validate the dynamic VAR behavior claimed by the authors.
Relation To Broader Scientific Literature: This paper contributes to the growing body of work at the intersection of classical statistical models and deep learning architectures. By drawing a connection between Vector Autoregressive (VAR) structures and linear Transformer models, the authors offer a novel perspective on how autoregressive attention mechanisms can be restructured to align with traditional time series modeling principles. If the empirical results are verified, the proposed SAMoVAR model could represent a meaningful step forward in the design of interpretable and effective models for time series forecasting (TSF), potentially influencing future research in both the deep learning and econometrics communities.
Essential References Not Discussed: While not strictly required, given the popularity and rapid development in time series forecasting (TSF), it would be helpful for the authors to discuss very recent advances in the field. One such example is TimeMixer++: A General Time Series Pattern Machine for Universal Predictive Analysis by Wang et al., recently accepted at ICLR 2025. This work proposes a highly general and competitive TSF model, and a comparison—either empirical or conceptual—would help situate SAMoVAR more clearly within the current landscape of TSF methods.
Other Strengths And Weaknesses: No additional strengths or weaknesses beyond those already discussed.
Other Comments Or Suggestions: No additional comments or suggestions.
Questions For Authors: 1. Comparison to Recent SOTA Methods: Given the likely overlap between the authors of this paper and the recent CATs model, could the authors provide more discussion or empirical comparison to other recent strong TSF methods such as TimeMixer++ (ICLR 2025)? A clearer comparison would help better position SAMoVAR in the current TSF landscape.
2. Why SAMoVAR Works Better Than CATs: While the paper clearly explains how SAMoVAR is constructed, it is less clear why it performs better than prior models like CATs. Could the authors elaborate on the intuition or mechanisms that drive the performance gains?
3. Clarification of Table 8 (Compute Efficiency): The reported FLOPs in Table 8 appear to be inconsistent or counterintuitive for several models. Could the authors clarify how these values were computed and confirm their correctness? A more transparent explanation would improve the credibility of the compute efficiency claims.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: >Performance differ from those presented in original papers ...
Thank you for your valuable question. For each baseline and output length $ L_P $, we run experiments with input lengths $ L_I \in \{512, 1024, 2048, 4096\} $ and report the best result. This avoids biases from models' sensitivity to input length, as noted in prior work. Our reported results may outperform those in the original papers, but never underperform. This evaluation strategy, also used in TiDE (https://arxiv.org/abs/2304.08424), ensures fairer and more strict comparison. Our problem setup follows DLinear, PatchTST, and iTransformer, and can be verified in our code repository (see `baseline.sh`).
```bash
for pred_len in 96 192 336 720
do
for seq_len in 4096 2048 1024 512
do
...
```
>Computational efficiency is less clearly supported
>Including formal analysis or clearer theoretical justification would strengthen the paper’s contribution.
Thank you for the suggestion. Our writing style follows prior work of LinTrans (e.g., Katharopoulos et al., 2020; Yang et al., 2024), focusing more on structure derivations and insights. We’re happy to add rigorous proofs of computational efficiency in the revision. Please see below:
**Proposition** SAMoVAR Attention has $ O(L) $ complexity with respect to sequence length $ L $.
**Proof** We analyze Algorithm 1 (SAMoVAR) in the appendix. Let batch size be $ B $, model dimension $ D $, number of heads $ H $, per-head dimension $ d = D/H $, and number of attention layers $ L_{\text{attn}} $.
**Preprocessing**:
- **LU Matrix Generation**: Creating the invertible matrix $ \mathbf{D} $ via LU decomposition is independent of $ L $, with cost $ O(Hd^2) $ per layer.
**Per-Layer Operations** (for each $ l = 1, ..., L_{\text{attn}} $):
1. **Linear Projections**: Computing $ Q^{(l)} $ and $ V^{(l)} $ costs $ O(LD^2) $.
2. **Cumulative State Update**: Recursively updating
$$
W_t = W_{t-1} + K_t \otimes V_t^{(l)}
$$
costs $ O(Hd^2) $ per step, totaling $ O(LHd^2) = O(LD^2/H) $.
3. **Output Computation**:
$$
Y_t = Q_t^{(l)} \otimes W_t
$$
also costs $ O(LD^2/H) $.
**Structural Transformation**:
$$
Y_{t,\text{transformed}} = \text{einsum}('bhd,hde \rightarrow bhe', Y_t, \mathbf{D}^{-1})
$$
has the same cost: $ O(LD^2/H) $.
**Conclusion**: Each layer has total cost $ O(LD^2) $. Since the number of layers is constant, overall complexity is $ O(LD^2) $, linear in sequence length $ L $.
>Comparison with TimeMixer++
Thank you for the suggestion. We added a comparison with TimeMixer++ at [Link (Table 2)](https://anonymous.4open.science/r/SAMoVAR-Rebuttal-F83C), using its official implementation and hyperparameters from `TimeMixer_ETTh1_unify.sh`. We evaluated all $ L_I \in \{512, 1024, 2048, 4096\} $. Note that the $ L_I = 512 $ result here outperforms the original $ L_I = 96 $ result. Our findings show that TimeMixer++ have no robust advantage over prior baselines and performs worse at longer $L_I$, similar to patterns seen in the DLinear and PatchTST papers. Interestingly, while recent NLP models trend toward longer contexts, recent TSF models (e.g., iTransformer, TimeMixer++) keep $ L_I $ as 96, compared to 512 in PatchTST, which is counterintuitive given TSF data (on test set) is typically continuous and not limited the usage of long context. We hope our varying $ L_I $ setup encourages a shift for TSF community toward the standards in line with broader sequence modeling area.
>Why SAMoVAR Better Than CATS
Thank you for the insightful question. Our results show that LinTrans with ARX tokenization performs closely to CATS, suggesting that autoregressive loss (as short-context data augmentation) and varying-context multitask training allow linear attention to match MLP-based models.
SAMoVAR goes further by explicitly modeling the VAR data generation process of MLP-constructed input sequences. You can view its MLP module as linearizing ARX-tokenized inputs, enabling dynamic VAR modeling via aligned linear attention. This offers a stronger inductive bias for TSF by better capturing lag, cycles in time series patterns compared to LinTrans.
>Clarification of Table 8 (Efficiency)
The computational costs in Table 8 align with our analysis. FLOPs and parameter counts are measured on ETTh1 with $ L_I = 512 $ for baselines and $ L_I = 1024 $ for linear attention models. All other hyperparameters follow the original ETTh1 settings.
For linear attention variants, we set hidden dimensions as $ d = \text{int}(32 \sqrt{C}) $; with $ C=7, d = 64 $, this results in fewer parameters than PatchTST/iTransformer (128/256).
SAMoVAR further reduces cost by removing all key projection matrices and sharing all output matrices $ \mathbf{W}_o $, leading to lower computational cost than LinTrans. FixedVAR, while having more parameters due to fixed weights per lag, avoids dynamic weight generation and thus has lower FLOPs than LinTrans.
In summary, Table 8 fully aligns with our analysis. | null | null | null | null |
Tree-Sliced Wasserstein Distance with Nonlinear Projection | Accept (poster) | Summary: The authors introduce the following:
1. Generalized Radon transforms in the system of lines.
- These transforms extend the concept of the Radon transform by incorporating systems of lines and allowing for nonlinear projections, which improve the flexibility and applicability of the SW distance.
2. Generalized Tree-sliced Wasserstein distance.
- The authors develop two specific variants of TSW—the Circular Tree-Sliced Wasserstein distance and the Spatial Tree-Sliced Wasserstein distance, which offer more efficient metrics for measures on both Euclidean spaces and spheres.
3. Applied generalized tree-sliced Wasserstein distance in generative model and gradient flow problems.
In addition, the new distance is applied for spherical data (Gradient flow and self-supervised learning).
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: New concepts:
- Generalized Radon transform in line system (Section 3.1, Eq(9)) and related injective property (Theorem 4.2-4.4)
- non-linear tree sliced Wasserstein distance (Eq (17), (18)) and metric property (Theorem 5.3)
- Additional RSpatial Spherical Radon Transform on Spherical Trees
Experimental Designs Or Analyses: Yes. I've checked the experiment design.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: **References:**
Kolouri, S., Park, J., & Rohde, N. (2019). Generalized Sliced Wasserstein Distances. arXiv preprint [arXiv:1906.06962](https://arxiv.org/abs/1906.06962).
Bonet, C., Berg, P., Courty, N., Septier, F., & Drumetz, L. (2022).
Spherical Sliced-Wasserstein.
arXiv:2206.08780 | PDF
DOI: 10.48550/arXiv.2206.08780
Tran, H., Bai, Y., Kothapalli, A., Shahbazi, A., & Liu, X. (2024).
Stereographic Spherical Sliced Wasserstein Distances.
arXiv:2402.02345 | PDF
DOI: 10.48550/arXiv.2402.02345
Leluc, R., Dieuleveut, A., Portier, F., & Segers, J. (2024).
Sliced-Wasserstein Estimation with Spherical Harmonics as Control Variates.
arXiv:2402.01493 | PDF
DOI: 10.48550/arXiv.2402.01493
Relation: Previous works have explored the combination of the generalized Radon transform/spherical Radon transform with the Wasserstein distance. This paper examines the application of the generalized Radon transform/spherical Radon transform to a system and analyzes the corresponding Wasserstein distance.
Essential References Not Discussed: Bonet, C., Berg, P., Courty, N., Septier, F., & Drumetz, L. (2022).
Spherical Sliced-Wasserstein.
arXiv:2206.08780 | PDF
DOI: 10.48550/arXiv.2206.08780
Leluc, R., Dieuleveut, A., Portier, F., & Segers, J. (2024).
Sliced-Wasserstein Estimation with Spherical Harmonics as Control Variates.
arXiv:2402.01493 | PDF
DOI: 10.48550/arXiv.2402.01493
Other Strengths And Weaknesses: ### Weaknesses:
1. It seems that any continuous injective function \( h \) can be used to define the generalized Radon transform. However, the criteria for selecting a suitable \( h \) for different datasets or tasks remain unclear.
In Section 5.2, the authors explain that \( h(x) \) can be determined by a neural network, but the structure and size of the neural network are not specified.
2. When \( h \) is implemented as a neural network, the cost of optimizing its parameters is not included in the computational complexity analysis in Section 5.3. This suggests that the actual complexity should be higher than the proposed value.
Additionally, in Figure 2, the computational cost of circular TSW appears to increase significantly when \( n \geq 400 \), but no explanation for this behavior is provided.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. The Circular Radon Transform (Equation (9)) is defined in \(\mathbb{R}^d\) rather than in a circular space. Could you clarify why it is referred to as the Circular Radon Transform?
Additionally, what is the reasoning behind the significant reduction in computational cost when using the Circular Radon Transformed Sliced-Wasserstein distance?
Code Of Conduct: Affirmed.
Overall Recommendation: 4
Ethical Review Concerns: N/A | Rebuttal 1:
Rebuttal: We direct the Reviewer to Tables R1-2 and Figure R1, available at https://sites.google.com/view/nonlinear-tsw-4.
**Q1. It seems that any continuous injective function $h$ can be used to define the generalized Radon transform. However, the criteria for selecting a suitable $h$ for different datasets or tasks remain unclear.**
**Answer Q1.** We kindly refer the Reviewer to our response to **Q1+W1** in Reviewer m8Ge's review.
**Q2. In Section 5.2, the authors explain that $h(x)$ can be determined by a neural network, but the structure and size of the neural network are not specified.**
**When $h$ is implemented as a neural network, the cost of optimizing its parameters is not included in the computational complexity analysis in Section 5.3. This suggests that the actual complexity should be higher than the proposed value.**
**Answer Q2.** A potential neural network for implementing $h(x)$ can be inspired by [6], where the neural network is a single feedforward layer that maps $\mathbb{R}^d \to \mathbb{R}^d$. Such a layer would have $d \times d$ weights and $d$ biases, introducing $O(d^2)$ parameters. If $h$ is implemented as a neural network, the cost of optimizing its parameters would scale the overall complexity linearly by the number of optimization steps. Incorporating learnable parameters into $h$ could enhance performance by better adapting to the data distribution, but it substantially increases the computational cost.
In our work, efficiency is a major concern, so we opted for a simple mapping to avoid this overhead. Specifically, for SpatialTSW, we use the mapping $h(x) = (f_1(x), \ldots, f_d(x))$, where $f_i(x) = x_i + x_i^3$. This mapping costs $O(n \cdot d_{\theta})$, which is trivial compared to other steps like projection or sorting.
**Q3. What is the reasoning behind the significant reduction in computational cost when using the Circular Radon Transformed Sliced-Wasserstein distance?**
**Additionally, in Figure 2, the computational cost of circular TSW appears to increase significantly when $n \geq 400$, but no explanation for this behavior is provided.**
**Answer Q3.** The significant reduction in computational cost when using the Circular Sliced Wasserstein variants arises from the efficiency of computing $L_2$ norms compared to inner products. This advantage is illustrated in Figure R1.
As shown in Figure 2, the computational cost of $CircularTSW_{r=0}$ increases when $n \geq 400$. This behavior is attributed to the cost of computing the splitting map $\alpha$, which remains $\mathcal{O}(L k n d_{\theta})$ — the same complexity as other tree-sliced variants. While $CircularTSW_{r=0}$ is theoretically and empirically more efficient in the projection and sorting steps, the cost of computing $\alpha$ becomes dominant as the number of support points $n$ grows.
In practice, $CircularTSW_{r=0}$ is slower than standard SW when the number of supports increases significantly since it involves the additional computation of the splitting map $\alpha$, whereas SW does not. However, in a large-scale experiment such as a diffusion model, $CircularTSW_{r=0}$ increases training time by only $12$\% compared to SW while substantially improving the FID from $3.64$ to $2.48$, highlighting a favorable practical trade-off. Additionally, $CircularTSW_{r=0}$ outperforms the best existing tree-sliced method, Db-TSW, in training time and FID.
**Q4. The Circular Radon Transform (Equation (9)) is defined in $\mathbb{R}^d$ rather than in a circular space. Could you clarify why it is referred to as the Circular Radon Transform?**
**Answer Q4.** The term circular refers to the circular defining function used in the Radon Transform, rather than the domain of the space itself. This naming convention is consistent with several prior works (see [4], [5]).
In contrast, for distances involving measures defined on the sphere, the term spherical is typically used (see [1], [2], [3]).
---
We thank the Reviewer for the constructive feedback, as well as for pointing out typos and missing references, which we will address. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
---
*References.*
[1] Hoang Tran et al., Spherical Tree-Sliced Wasserstein Distance, ICLR 2025.
[2] Clément Bonet et al., Spherical Sliced-Wasserstein, ICLR 2023.
[3] Huy Tran et al., Stereographic Spherical Sliced Wasserstein Distances, ICML 2024.
[4] Soheil Kolouri et al., Generalized Sliced Wasserstein Distances, NeurIPS 2019.
[5] Gaik Ambartsoumian et al., On the injectivity of the circular Radon transform, Inverse Problems 21 (2005).
[6] Xiongjie Chen et al., Augmented Sliced Wasserstein Distances, ICLR 2022. | Summary: This work proposes to extend the Tree Sliced-Wasserstein distances, defined using linear projections on system of lines, by using nonlinear projections instead. The authors study the use of two different non linear projections: circular projections and spatial projections. They also propose to use a spatial projection on the sphere. Then, they introduce the associated Radon transform on system of lines, show that they are injective, define the resulting Tree-Sliced Wasserstein distances and show that these are well distances. Finally, they benchmark these distances on several applications such as generative modeling with Denoising Diffusion GANs and gradient flows for the Euclidean non linear projections, and gradient flows, self-supervised learning and Sliced-Wasserstein autoencoders for the spherical version.
## Update after rebuttal
I maintain my positive score.
Claims And Evidence: The claims made are well supported. The constructions proposed are well justified, and the proofs of the claims such as distance properties are provided.
Methods And Evaluation Criteria: The evaluation criteria to compare the new distances with previously proposed distances make sense.
Theoretical Claims: The proofs seem to be correct.
Experimental Designs Or Analyses: The experimental designs are good.
Supplementary Material: I read briefly the background parts of the supplementary materials.
Relation To Broader Scientific Literature: The key contribution of this paper is to extend the Tree Sliced-Wasserstein distance proposed in [1, 2] using non linear projections. Non linear projections were first used in [1] for the Sliced-Wasserstein distance. In particular, they leverage results from [2] to show that the proposed constructions are well distances.
The second key contribution is to extend the spherical Tree Sliced-Wasserstein distance proposed in [4] with non linear projections.
[1] Tran, V.-H., Pham, T., Tran, T., Le, T., and Nguyen, T. M. Tree-sliced wasserstein distance on a system of lines. arXiv preprint arXiv:2406.13725, 2024.
[2] Tran, H. V., Nguyen-Nhat, M.-K., Pham, H. T., Chu, T., Le, T., and Nguyen, T. M. Distance-based tree-sliced wasserstein distance. In The Thirteenth International Conference on Learning Representations, 2025.
[3] Kolouri, S., Nadjahi, K., Simsekli, U., Badeau, R., and Rohde, G. Generalized sliced wasserstein distances. Advances in neural information processing systems, 32, 2019.
[4] Tran, H. V., Chu, T., Nguyen-Nhat, M.-K., Pham, H. T., Le, T., and Nguyen, T. M. Spherical tree-sliced wasserstein distance. In The Thirteenth International Conference on Learning Representations, 2025.
Essential References Not Discussed: All the essential references seem to be discussed.
Other Strengths And Weaknesses: This paper introduces on one hand non linear projections to extend the Euclidean and Spherical Tree Sliced-Wasserstein distances, which are natural things to study. This paper is doing it well as it provides justifications to all the choices. However, the background is hard to follow, as it relies a lot on the previous papers [1,2,3], with a brief description in Appendix. This is the main limit that I found with the current state of this work.
**Strengths**:
- Provide new (Spherical) Tree SW distances using non linear projections, which are well distances. In particular, the Spatial Spherical TSW distance use a new projection.
- Several experiments showing benefits compared to other distances
**Weaknesses**:
- The paper feels a bit incremental, but there are lots of results, which compensate.
- The background is not very clear, and lot of important things to understand the paper are in Appendix. Also, more figures could help understanding the constructions.
- It is not really stated when one would prefer one type of non linear projection compared to another.
[1] Tran, V.-H., Pham, T., Tran, T., Le, T., and Nguyen, T. M. Tree-sliced wasserstein distance on a system of lines. arXiv preprint arXiv:2406.13725, 2024.
[2] Tran, H. V., Nguyen-Nhat, M.-K., Pham, H. T., Chu, T., Le, T., and Nguyen, T. M. Distance-based tree-sliced wasserstein distance. In The Thirteenth International Conference on Learning Representations, 2025.
[3] Tran, H. V., Chu, T., Nguyen-Nhat, M.-K., Pham, H. T., Le, T., and Nguyen, T. M. Spherical tree-sliced wasserstein distance. In The Thirteenth International Conference on Learning Representations, 2025.
Other Comments Or Suggestions: I would suggest to try to improve the introduction of the background on the Tree SW distances, and to add Figures to better understand how the projections work. For instance, in Section 3.2, the Radon transforms on System of Lines are introduced, but all notations do not seem to be introduced (e.g. it is not clear directly what is $\mathbb{L}_k^d$).
In Figure 1, it is not directly clear what is projected, what is $x_i$... It would be better to add a legend on the Figure with labels on the points projected and the center $x_i$. Also, it would maybe help to see a comparison with $r>0$.
In Section 5, it is stated that explanations are provided for the choice of the projections, and why they lead to more efficient metrics, but it is not very clear where it is stated after.
In Figure 2, the result are given for $n$ up to $n=500$, which is rather small for sliced settings.
In Table 2 and 3, this is basically the same experiment, but the results are not provided in the same way ($W_2$ versus $\log_2 W_2$).
Typos:
- Line 204, 1st column: "$R^n$"
- Line 215, 2nd column: "We also examine different choices of functions that define the nonlinear projections explain why certain choices lead to more efficient metrics."
- Line 293, 1st column: "$f_i(x)=x_i+x_i^3$"
- Line 383, 2nd column: "Inspised"
Questions For Authors: 1. You are proposing new choices for the polynomials $h$: how does it compare to the construction proposed in [1]?
2. How the trees are constructed? I am not sure it is precised (but I may have missed it)
[1] Kolouri, S., Nadjahi, K., Simsekli, U., Badeau, R., and Rohde, G. Generalized sliced wasserstein distances. Advances in neural information processing systems, 32, 2019.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We direct the Reviewer to Table R1-2 at https://sites.google.com/view/nonlinear-tsw.
**Q1. The paper feels a bit incremental, but there are lots of results, which compensate.**
**It is not really stated when one would prefer one type of non linear projection compared to another.**
**Answer Q1.** We kindly refer the Reviewer to our response to **Q1+W1** in Reviewer m8Ge's review.
**Q2. You are proposing new choices for the polynomials $h$: how does it compare to the construction proposed in [1]?**
**Answer Q2.** In [1], the author proposed using homogeneous polynomials of odd degree for the mapping $h: \mathbb{R}^d \to \mathbb{R}^{d_\theta}$, where the output dimension $d_\theta$ grows exponentially with $d$. For large $d$, such as in our Diffusion Experiment where $d \approx 3000$, this results in $d_\theta \approx 4.5 \times 10^9$ (see line 263-270), making the approach computationally impossible. In contrast, our proposed mapping, defined as $h(x) = (f_1(x), \ldots, f_d(x))$ with $f_i(x) = x_i + x_i^3$, maintains the same output dimension as the input ($d_\theta = d$) and introduces a trivial computational cost while still ensuring a non-linear projection.
**Q3. How the trees are constructed? I am not sure it is precised (but I may have missed it)**
**Answer Q3.** The tree structure used in our paper is the concurrent-lines structure introduced in [2]. We will make this explicit in the revised version of the paper.
**Q4. The background is not very clear, and lot of important things to understand the paper are in Appendix. Also, more figures could help understanding the constructions.**
**Answer Q4.**
We acknowledge that the background for the tree-sliced approach can be dense, as it builds upon the foundations laid in [2] and [4]. We thank the Reviewer for pointing this out and will revise the paper to include additional figures to improve readability.
**Q5. In Figure 2, the result are given for $n$ up to $n=500$, which is rather small for sliced settings.**
In Figure 2, we use $n$ up to $500$ because Diffusion Model experiments typically train with batch sizes $n < 500$. Additionally, we set $d = 3000$, $L = 2500$, and $k = 4$, aligning with the practical settings of the Diffusion Model experiment. We also provide runtime and memory analysis for our Tree-Sliced Wasserstein variants in Appendix D.3, with $n$ up to $50000$.
**Q6. In Table 2 and 3, this is basically the same experiment, but the results are not provided in the same way ($W_2 \text{ versus } \log_2 W_2$).**
Table 2 is about Gradient Flow on Euclidean space $\mathbb{R}^d$, while Table 3 is about Gradient Flow on the sphere $\mathbb{S}^d$. Therefore, the choice of experimental setting and baselines are different. Note that Table 2 follows the setting of [2], while Table 3 follows the setting of [4].
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We thank the Reviewer for the constructive feedback, as well as for pointing out typos and missing references. We will address them accordingly. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
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*References.*
[1] Soheil Kolouri et al., Generalized Sliced Wasserstein Distances. NeurIPS 2019.
[2] Hoang Tran et al., Distance-Based Tree-Sliced Wasserstein Distance, ICLR 2025.
[3] Hoang Tran et al., Tree-Sliced Wasserstein Distance on a System of Lines.
[4] Hoang Tran et al., Spherical Tree-Sliced Wasserstein Distance, ICLR 2025.
[5] Tam Le et al., Tree-Sliced Variants of Wasserstein Distances, NeurIPS 2019.
[6] Tam Le et al., Sobolev Transport: A Scalable Metric for Probability Measures with Graph Metrics, AISTATS 2022.
[7] Makoto Yamada et al., Approximating 1-Wasserstein Distance with Trees, TMLR 2022. | Summary: This paper extends the Tree-Sliced Wasserstein (TSW) distance, an alternative to the Sliced Wasserstein (SW) distance that leverages tree-based metric spaces, by allowing the use of nonlinear projections. More precisely, the authors explore generalized Radon transforms (previously used in existing SW variants, such as Generalized SW by Kolouri et al. (2019) or Augmented SW by Chen et al. (2022)), and analyze how these can be integrated into TSW while preserving injectivity and invariance properties. This analysis leads to the definitions of two instances of TSW, called "Circular Tree-Sliced Wasserstein Distance" and "Spatial Tree-Sliced Wasserstein Distance". Finally, they apply these new metrics to generative models, gradient flows and self-supervised learning, to compare the result quality and computational efficiency against SW and variants.
Claims And Evidence: The theoretical and methodological contributions of this paper seem sound to me, as they naturally extend related work by combining results from SW based on nonlinear projections and tree-based SW. That said, some imprecise points remain and could be addressed (see section 'Theoretical Claims').
My biggest concern is with the empirical analysis and conclusions. In my opinion, the authors make overclaims that are not properly justified by solid and convincing evidence: instead of providing a more nuanced description of the obtained results, they draw conclusions that seem overstated to me. See my detailed comments in "Methods and Evaluation Criteria" and "Experimental Designs or Analyses".
Methods And Evaluation Criteria: The experiments in this paper involve incorporating different metrics into existing black-box machine learning pipelines, whose behavior is hard to interpret. As a result, directly comparing the performance of different variants is challenging, and the analysis relies solely on quantitative scores such as FID, which I find insufficient to illustrate the authors' strong conclusions.
I think the paper would be significantly more convincing if the authors identified a simpler and more interpretable setting where their proposed non-linear tree SW metrics demonstrably capture relevant data features more efficiently. Such a well-chosen controlled experiment could provide more insights into the advantages of their approach, that nicely complement the current empirical analysis.
Theoretical Claims: I skimmed through the proofs in the supplementary document. The theoretical claims appear to be adaptations of results from the literature on generalized/augmented SW and tree SW, with these extensions facilitated by the linear operations in the tree structure.
The authors focus on the first-order ($p = 1$) case, justifying this choice by stating: "For simplicity, the focus is on measures with a finite first moment, while measures with a finite $p$th-moment are treated analogously." (l.85-88) However, the treatment of $p>1$ is not as trivial as suggested when establishing the metric properties, injectivity, and well-definedness.
Experimental Designs Or Analyses: The authors claim that the proposed tree-sliced-Wasserstein distances "consistently outperform state-of-the-art Sliced Wasserstein and Tree-Sliced Wasserstein methods across various tasks" and support this point with a series of experiments (Section 6 and supplementary doc). However, I find the empirical results not convincing enough:
- Across all experiments, the improvement in precision appears marginal (see Tables 1-5), and there is no uncertainty quantification. Additionally, the only qualitative results available (Figure 7 in the supplementary document) do not clearly demonstrate the advantages of the proposed tree-sliced metrics in terms of image generation quality.
- The authors state that their approach "maintains comparable or improved runtime efficiency" and specifically, they report that "CircularTSW-DD and CircularTSW reduce training time relative to Db-TSW-DD⊥ by 10% and 19%, respectively" and "CircularTSW and CircularTSWr=0 are approximately 5% and 16% faster than vanilla SW, respectively". While these claims are accurate, the results in Tables 1 and 2 reveal the reduction in computation time is negligible: CircularTSW and CircularTSWr=0 take 0.0017s and 0.0015s per iteration, respectively, compared to 0.0018s for SW. Furthermore, the results lack consistency across experiments: in Table 1 and Table 5, vanilla SW is the first or second fastest method.
Supplementary Material: I read the supplementary material, but did not thoroughly check the proofs.
Relation To Broader Scientific Literature: The key contribution of this paper is the combination of non-linear projections in sliced optimal transport with the tree structure. Both the theoretical results and experimental designs build on existing literature in this area, and the technical challenges involved in integrating these prior works are not sufficiently emphasized.
Essential References Not Discussed: The related works is adequately discussed. Some references that are relevant and seem to be missing are:
- "Parallelly Sliced Optimal Transport on Spheres and on the Rotation Group", M. Quellmalz, L. Buecher, G. Steidl (2024)
- "Sliced Optimal Transport on the Sphere", M. Quellmalz, R. Beinert, G. Steidl (2023)
Other Strengths And Weaknesses: I find the paper lacks clarity and rigor:
- Several key definitions are missing from the main text, making it difficult to read and understand (see "Other comments or suggestions" for details).
- Some strong claims about important aspects of the method lack proper and precise justification. For instance, the notions of well-definedness and injectivity (l.134) are not properly defined, and it is unclear why "injectivity is typically required for Radon Transform variants". Remark 3.2 presents intriguing, non-trivial information, without supporting results or references: why does $\alpha$ induce a tradeoff between effectiveness and theoretical guarantees, , and what kind of guarantees are being referred to? In what sense "the distances derived from RTSL surpass those obtained from the original Radon Transform"?
Other Comments Or Suggestions: - l.98: the definition of the set $L^1(\cdot)$ is missing
- l.107: missing definition for $\mathcal{U}(\mathbb{S}^{d-1})$
- Missing definition for $\theta_\sharp$ (Section 2)
- l.102 : $\mathbb{R}_{\geq 0}$ can be written $\mathbb{R}_+$
- Section 3.2: all the notations given in Section A to define tree-sliced SW should be recalled in that section.
- Equation (14): the operation $gy,g\mathcal{L}$ is unclear in the main text: equation (66) should appear earlier.
- l.709: "Sysmtes"
- Section 6.2: "Inspised"
Questions For Authors: Given my comments above, the proposed nonlinear tree SW variants seem to be incremental extensions of existing methods. This lack of novelty, in some sense, would not be problematic if the contributions yield clear advantages on other aspects, for instance here in terms of practical performance. However, in my opinion, this is not sufficiently achieved in the current work.
Therefore, I would appreciate if the authors could:
- Explicitly highlight the technical challenges involved in developing this approach or in establishing its theoretical guarantees, particularly in comparison to prior work.
- Design a simpler, more interpretable experiment (e.g., based on synthetic data) where the advantages of their proposed methods are more clearly demonstrated.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We direct the Reviewer to Table R1-4 and Figure R1 at https://sites.google.com/view/nonlinear-tsw-2.
**Q1. Explicitly highlight ... to prior work.**
**Answer Q1.** The key technical challenge in developing this approach lies in proving the injectivity of the proposed Radon Transforms, which ensures that the resulting distances qualify as proper metrics. This differs from prior work on TSW, such as [2]. Compared to SW approaches—including those that also employ nonlinear projection techniques like [1]—the difference is even more pronounced due to the introduction of splitting maps $\alpha$.
Given these factors, we believe our approach to addressing these challenges is non-trivial.
**Q2. The notions of well-definedness ... Radon Transform variants".**
**Answer Q2.** The two mentioned properties above hold under certain assumptions on the functions $g$ and $h$, such as continuity, smoothness, and injectivity. These conditions have been discussed in previous works (see lines 134–144).
In our work, we do not elaborate on these general assumptions; instead, we provide specific types of functions that satisfy the necessary conditions for our method. A detailed discussion of why these functions meet the required properties are presented Section 4.2 and Appendix B.
Injectivity is typically required for variants of the Radon Transform because it ensures that the derived metrics are proper metrics rather than pseudo-metrics.
**Q3. In what sense ... Radon Transform?**
**Q4. Why does $\alpha$ ... being referred to**
**Answer Q3+Q4.** Previous works on TSW [2, 3, 4] show that replacing lines in the SW framework with tree structures via the splitting mechanism $\alpha$ consistently enhances performance, even with the same number of projections.
Notably, $\alpha$ is independent of SW components, suggesting that other SW improvements could be integrated into the tree-sliced framework. However, verifying well-definedness and injectivity in this new setting requires novel analytical approaches.
**Q5. Design a simpler ... clearly demonstrated.**
**Answer Q5.** The non-linearity in SpatialTSW complicates the design of settings where it outperforms other variants. Empirically, SpatialTSW matches Db-TSW (see Tables 1, 2, and R1), suggesting it as a drop-in replacement for Db-TSW with potential performance gains.
We provide intuition for when CircularTSW and CircularTSW$_{r=0}$ may outperform other variants. Since these distances rely on the $L_2$ norm for projection, they are likely to excel when the $L_2$ norms of the data are diversely distributed. We validate this advantage over Db-TSW and SpatialTSW in Table R2 on a synthetic dataset. The improvement is more pronounced for high-dimensional data (large $d$), indicating that variants using circular defining functions perform well while others struggle in such settings.
**Q6. Across all experiments, ... image generation quality.**
**Answer Q6.** In our paper, uncertainty quantification for Table 2 is provided in the Appendix (see Table 7). We also include uncertainty quantification for the Diffusion Model and SWAE experiments in Tables R3 and R4, respectively.
We provide a new qualitative result for Point Cloud Gradient Flow, visualizing the faster convergence of SpatialTSW in Figure R1.
**Q7. The authors focus on the first-order ... and well-definedness.**
**Answer Q7.** For $p>1$, the proposed approach can be extended. However, the Tree-Wasserstein distance with $p>1$ lacks a closed-form solution (see [5]). A meaningful alternative is provided by Sobolev Transport (ST) [6], which offers a closed-form solution and has been applied in the tree-sliced framework, as discussed in [3, Eq. (15)].
Although TSW works such as [2] and [4] do not explicitly address this aspect, their implementations support arbitrary $p>1$. We omit the complex ST literature to reduce presentation complexity while keeping implementation flexible, and thus chose not to include it.
Due to space constraints, we strongly encourage the Reviewer to refer to the ST literature [6]. Based on its properties, our extension to the $p>1$ case satisfies the theoretical guarantees previously discussed.
**Q8. The results in Tables 1 and 2 ... is negligible**
**Answer Q8.** We acknowledge that the reduction in computation time in Table 2 is marginal, as this experiment uses a toy synthetic dataset. However, in Table 1, when applied to real-world Diffusion Models, CircularTSW$_{r=0}$ reduces the total training time to 105.5 hours compared to 131 hours for Db-TSW over 1800 epochs, saving 25.5 hours of computation time.
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We thank the Reviewer for the constructive feedback, as well as for pointing out typos and missing references, which we will address. If our clarifications are satisfactory, we kindly ask you to consider raising the score. We are happy to address any further concerns in the next discussion stage.
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*References.* Kindly refer to **References** in our response to Reviewer jNth. | Summary: The authors introduce several new variants of tree-sliced Wasserstein distance, which was introduced in [TPTLN '24]. This is done via two new proposed Radon transforms: (1) the generalized Radon transform on systems of lines and (2) the spatial Radon transform on systems of lines. Using their new Radon transforms, the authors define two variants tree-sliced Wasserstein distance: (1) circular tree-sliced Wasserstein (CircularTSW) distance and (2) spatial tree-sliced Wasserstein (SpatialTSW) distance. Unlike previous work, which used linear projections to construct tree-sliced Wasserstein distance, CircularTSW and SpatialTSW incorporate non-linear projections.
"Tree-sliced wasserstein distance on a system of lines" [TPTLN '24]
### Update after rebuttal
Thanks to the authors for their response. I maintain my score.
Claims And Evidence: All claims/theorems are supported by proofs.
Methods And Evaluation Criteria: The benchmark datasets seem reasonable to me.
Theoretical Claims: I did not check the proofs.
Experimental Designs Or Analyses: I checked the experimental design and it seems reasonable to me.
Supplementary Material: I did not review the supplement.
Relation To Broader Scientific Literature: This paper is a follow up to [TPTLN '24] and [TCNLN '25]. While [TPTLN '24] introduces the general tree-sliced Wasserstein distance on systems of lines, this work extends it by introducing generalized Radon transforms on systems of lines and defining the corresponding tree-sliced Wasserstein distances. The current paper extends previous work by integrating nonlinear projection mechanisms, which allow for more flexible and expressive transformations of probability measures.
"Distance-based tree sliced Wasserstein distance" [TCNLN '25]
Essential References Not Discussed: I do not know of any essential references which are not discussed.
Other Strengths And Weaknesses: Strengths: The authors present a novel extension of the previous tree-sliced Wasserstein distance to use non-linear projections. These new tree-sliced Wasserstein distance variants may help better encode topological information than tree-sliced Wasserstein with linear projection. They also present extensive experiments that highlight the strength of their new tree-sliced Wasserstein variants.
Weaknesses: Given that there are so many variants of TSW, the authors could maybe motivate a bit more why/when CircularTSW or SpatialTSW will outperform SW or TSW with linear projection.
Other Comments Or Suggestions: You use the abbreviation for Circular Radon Transform on Systems of Lines (CRTSL) but you forgot to add the parenthetical defining the abbreviation above Eq. 10.
Questions For Authors: 1. Is there any intuition for when each tree-sliced Wasserstein distance should be used? It seems now that is a large zoo of tree-sliced Wasserstein distances but I am unsure when I should use one tree-sliced Wasserstein distance over another.
2. How should I select $r$ for CircularTSW? How does the choice $r$ affect performance empirically?
3. It seems like this tree-sliced Wasserstein distance on systems of lines can be very general. Is there a way to define a general tree-sliced framework that will include both CRT and SRT?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We direct the Reviewer to Table R1-2 at https://sites.google.com/view/nonlinear-tsw.
**W1. [...] (many variants of TSW) outperform SW or TSW with linear projection**
**Q1. [...] (intuition) one (TSW) over another**
**Answer.** Our motivation for proposing the non-linear projection framework is inspired by Generalized Sliced-Wasserstein (GSW) [1], which also includes both Circular and Spatial variants. It is underexplored in prior studies that among the three versions—original SW, SpatialSW, and CircularSW, which variant is most suitable for a given task.
This suggests that among the corresponding TSW variants—Db-TSW [2], CircularTSW, and Spatial TSW—there is no guarantee that the versions with non-linear projections will consistently outperform the linear-projection TSW. However, the two new distance variants each offer distinct advantages over standard TSW, as outlined below:
- The definition of SpatialTSW subsumes Db-TSW as a special case when the function $h$ is the identity map (see lines 122–124). This implies that models leveraging SpatialTSW have, in theory, greater representational capacity than those using Db-TSW. A similar relationship holds between the corresponding SW variants.
- The definition of CircularTSW is theoretically non-comparable to Db-TSW due to their fundamentally different constructions. However, $CircularTSW_{r=0}$ offers improved runtime efficiency. This benefit does not hold in the SW context, where $CircularSW_{r=0}$ performs poorly (see lines 252–261). One reason is that $CircularSW_{r=0}$ defines only a pseudo-metric, while $CircularTSW_{r=0}$ is a true metric.
Our framework offers greater flexibility by enabling a broader selection of distance functions. However, in Machine Learning, predicting the best variant for a task often requires empirical experimentation. Table R1 shows that both Db-TSW and SpatialTSW perform well, but the non-linearity in SpatialTSW makes it hard to determine in advance which variant is better suited for a given task.
We offer intuition for selecting CircularTSW and $CircularTSW_{r=0}$. Since these distances rely on the $L_2$ norm for the projection step, they are likely to perform well when the $L_2$ norms of the data are diversely distributed. We validate this advantage over Db-TSW and SpatialTSW in Table R2, where the distribution of $L_2$ norms is uniform. We speculate that this property explains why CircularTSW performs effectively for the Diffusion experiment (Table 1).
To the best of our knowledge, Db-TSW [2] is the only tree-sliced distance effectively suited for large-scale generative tasks involving transport from a training measure to a target measure in Euclidean space. Previously, [3] presents a basic and limited version of [2], primarily emphasizing the constructive aspects of the tree-sliced approach, which serve as foundational groundwork. Meanwhile, [4] explores the method in a spherical setting. Other works on Tree-Sliced Wasserstein (TSW), such as [5], [7], and others, are mainly designed for classification tasks and are not applicable to generative settings. This limitation arises because these methods rely on a clustering-based framework for computing slices—which is theoretically unsuitable (as the clustering must be recomputed each time the training measure is updated, **rendering previous clustering results irrelevant**) and empirically inefficient (since clustering is significantly more computationally expensive than linear or non-linear projection methods).
**Q2. [...] (select $r$) affect performance empirically?**
**Answer Q2.** Selecting the optimal hyperparameter, such as $r$ for CircularTSW, is challenging and often requires empirical tuning. Intuitively, $r$ should be large enough to ensure diverse projections onto the lines but should not exceed the data's magnitude. For normalized data, we suggest starting with $r = \frac{1}{\sqrt{d}}$ and tuning from there.
**Q3. [...] (include) CRT and SRT?**
**Answer Q3.** The TSW-SL [3] offers more general tree structure than the concurrent-lines tree structure used in [2]. However, this generality comes at the cost of runtime efficiency, as the concurrent-lines structure allows a GPU-friendly implementation. Since efficiency is a priority in our work, we adopt the concurrent-lines structure.
When extending TSW-SL to non-linear projections, we initially believed SRT could apply to general tree structures, as key properties like injectivity are preserved. However, this does not seem to hold for CRT, since parts of the proof that CircularTSW defines a valid metric rely on the specific concurrent-lines structure.
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We thank the Reviewer for the constructive feedback and for pointing out the typos, which we will address. If our clarifications are satisfactory, we kindly ask you to consider raising the score. We are happy to address any further concerns in the next discussion stage.
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*References.* Kindly refer to **References** in our response to Reviewer jNth. | null | null | null | null | null | null |
Tightening Causal Bounds via Covariate-Aware Optimal Transport | Accept (poster) | Summary: The manuscript introduces a novel method for bounding treatment effects using covariate information, reframing the problem as an optimal transport task. Specifically, the authors propose adding a penalty term to the standard optimization objective that encourages covariates to have similar distributions in both treatment arms. They show that varying the weight of this penalty effectively interpolates between unconditional and conditional approaches. They study the statistical and computational aspects of their algorithm, which can be solved using linear programming, and present experimental benchmarks.
## update after rebuttal
I thank the authors for resolving a confusion on my part about their target estimand. I still have some reservations about the use of Neyman confidence intervals as a benchmark. In any event, I will maintain my score of 4.
Claims And Evidence: The primary claims of the paper are:
-under the stated assumptions, the interpolating OT lower bound exists and is unique;
-the interpolating OT lower bound is a monotonically increasing function of the penalty parameter $\eta$ and interpolates between unconditional ($\eta=0$) and conditional ($\eta= \infty$) OT lower bounds;
-the convergence rate of the estimator for this parameter is upper bounded by a well defined function of the sample size;
-the method performs well in experiments with simulated and real-data.
The first three claims, which are all theoretical in nature, are well articulated and generally convincing (although I have some questions about structural assumptions, see below). I find the experiments less compelling, as the only methods included in the benchmark are dualbounds (a relatively recent, seemingly unpublished method) and Neyman confidence intervals (which are not conditional and not intended to be partial identification intervals). Several other PI methods have been published in recent years that do not necessarily rely on optimal transport theory, and I would be curious to see how they stack up (more on this below).
Methods And Evaluation Criteria: The real and simulated datasets make sense, although I have a couple of comments/questions:
-The use of $d_Z$ in the description of the DGP (§5.2) suggests that multiple covariates are in play, but it appears from the code that this is fixed at 1. Unless I'm missing something?
-The Neyman CI approach is not really an apples-to-apples comparison, even to the unconditional PI. This conflates uncertainty from finite samples with uncertainty from the structure of the DGP itself. I would consider dropping this after other PI methods are incorporated.
Theoretical Claims: The mathematical reasoning appears clear and sound, although I confess I did not closely examine the proofs.
Experimental Designs Or Analyses: The experimental design seems sound, but see my comments above regarding relevant (and irrelevant) benchmarks.
Supplementary Material: I perused the appendix and code supplement. Both appear sound.
Relation To Broader Scientific Literature: This topic is of general interest to the causal inference community, and the method could have applications in econometrics and/or healthcare. Presentation would be aided by a running example of $W, Z, Y$ variables that could help ground the discussion.
Essential References Not Discussed: Some aspects of this manuscript are clearly quite thoroughly researched, featuring strong engagement with the contemporary literature. However, this is not the case when it comes to partial identification (even including Appx A1). Several methods have been proposed in recent years for bounding treatment effects under minimal assumptions, and I was surprised to see none featured in the benchmark experiments. For example:
-https://ojs.aaai.org/index.php/AAAI/article/view/17437
-https://proceedings.mlr.press/v162/zhang22ab.html
-https://proceedings.mlr.press/v213/padh23a.html
-https://proceedings.mlr.press/v235/jiang24b.html
-https://openreview.net/forum?id=OaJLMx2nwS
These may not all be equally relevant, but in any event the text should explain why and include at least some of these in the experiments. (With respect to IV models, it's not clear to me whether $Z$ may be considered a "leaky" instrument? More on this below.)
Other Strengths And Weaknesses: The paper is very clear and well-written. The mathematical results are rigorous and sound. I'm intrigued by this target estimand, which appears novel as far as I can tell. It's somewhere in between an ATE and a CATE, with $\eta$ controlling the degree of interpolation. Here's one way of stating this: $\tau(z, \eta) := \mathbb E[Y(1) - Y(0) \mid z + \mathcal N(0, \eta^{-2})]$. I know the present method doesn't commit us to any particular parametric assumptions the way this does, but am I correct in saying this formulation captures the spirit of the proposal? That is, $\tau(z, \eta)$ approaches the ATE as $\eta \rightarrow 0$, the CATE as $\eta \rightarrow \infty$, and something in between for all intermediate values. Of course, the goal here is *partial* identification rather than point identification, but I still find it helpful to have some idea just what the target estimand is that we're bounding.
Other Comments Or Suggestions: N/A
Questions For Authors: My main question pertains to what structural assumptions (if any) are in play regarding these covariates $Z$?
I will use graphical notation to spell out my questions, although I appreciate from the text that the authors are approaching this from the potential outcomes tradition.
Basically, I would like to know (a) whether the user is supposed to know the true parents/children of $Z$; and (b) which of the following graphs are fair game for this method:
(1) $Z \rightarrow X \rightarrow Y \leftarrow Z$
(2) $X \rightarrow Z \rightarrow Y \leftarrow X$
(3) $X \rightarrow Y \leftarrow Z$
(4) Anything else.
As an additional question, I would like to know precisely what assumptions are made regarding latent confounders? Apologies if this is stated somewhere in the text, but I could not find it.
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We highly appreciate the reviewers' summar and comments.
> Several other PI methods have been published in recent years that do not necessarily rely on optimal transport theory, ...
The other PI methods deal with the case where there is unobserved confounder/leaky IV, such that the observed marginal distributions of outcomes do not equal the true ones, thus needing PI. In contrast, we are interested in estimating a functional of the joint coupling of the outcomes, which is also partially identifiable and thus we seek PI through OT (a coupling theory). As a result, our PI and the other PI methods that the reviewer lists deal with different cases of partial identifiability, thus are not very relevant and cannot be compared in the our setting.
> It appears from the code that this is fixed at 1. Unless I'm missing something?
In the code, the input $d_Z$ for function *vip_estimate* can be set to any integer, for computing the true value of Vc or Vip, in the simulation result, we make the examples using $d_Z = 1$.
> The Neyman CI approach is not really an apples-to-apples comparison.
The Neyman CI approach is basically about the variance estimation of the outcomes from the sample, which is a standard estimand in causal inference. We use this as an example to show that the quadratic objective h is a practical one. Specifically, in [1], the tightest Neyman variance estimator without covariate information is the same as the optimal objective value of the associated OT problem, and our approach incorporates the covariate information in this formulation on top of their work.
> Some aspects of this manuscript are clearly quite thoroughly researched ... However, this is not the case when it comes to partial identification (even including Appx A1) …
Our PI and the other PI methods that the reviewer lists deal with different cases of partial identifiability.
In the reviewer’s list, due to hidden confounder / leaky instrumental variables, the observed marginal data distributions are different from the target marginal distribution.
(i) hidden confounder:
https://ojs.aaai.org/index.php/AAAI/article/view/17437
https://proceedings.mlr.press/v162/zhang22ab.html
https://proceedings.mlr.press/v213/padh23a.html
(ii) leaky instrumental variable:
https://proceedings.mlr.press/v235/jiang24b.html
https://openreview.net/forum?id=OaJLMx2nwS
In contrast, our PI is due to the unobserved joint coupling distribution of the outcomes in different treatment groups (i.e. *cross-world dependence*). Therefore, we utilize the framework of optimal transport to analyze the possible couplings of the observed cross-world outcomes. As a result, our PI approach and the other PI approaches the reviewer lists target different types of partial identifiability. In future work, we will investigate the combination of our PI and the other PIs, i.e., dealing with scenarios involving two sources of partial identifiabilities.
In the literature related to the PI relevant to our approach (PI on joint couplings), we have discussed several papers in the Appendix A. In the revised version, we will discuss the difference between our PI and the other PI that is more relevant to the reviewer’s list (e.g. [2]).
> I'm intrigued by this target estimand ... between an ATE and a CATE …
Our target estimand is different from ATE and CATE in that, in our randomized experiment setting, both ATE and CATE are identifiable ($E[Y(1) - Y(0)]$), while our target estimand $E[(Y(0) - Y(1))^2]$ is partially identifiable because it not only relies on the marginal distribution of $Y(0), Y(1)$, but more importantly depends on their unobserved joint distribution. Therefore, the nature of our target estimand and ATE (CATE) are different, thus our PI targets on the partial identifiability of coupling of outcomes, while other PI, particularly ATE, CATE, may focus on the the partial identifiability resulted by hidden confounders.
> (a) whether the user is supposed to know the true parents/children of Z and (b) which of the following graphs are fair game ...
We set $X$ to be treatment, $Y$ to be outcome, and $Z$ to be covariate.
In view of a causal diagram, our randomized experiment setting is: (3) $X \rightarrow Y \leftarrow Z$. Our approach can be extended to the case (1) $Z \rightarrow X \rightarrow Y \leftarrow Z$, i.e., allowing the covariates to influence the treatment assignment, by incorporating the propensity scores. We leave this direction for future research.
According to the DAG, we have: Z has no parents, and Y is the children of Z. Actually, for the vector variable Z, we allow an arbitrary structure inside the vector Z. In the paper,, we assume there are no latent confounders (Assp. 3.1).
[1] Aronow, Peter M., Donald P. Green, and Donald KK Lee. "Sharp bounds on the variance in randomized experiments." (2014): 850-871.
[2] Imbens, Guido W., and Donald B. Rubin. Causal inference in statistics, social, and biomedical sciences. Cambridge university press, 2015. | Summary: The paper investigates the problem of tightening partial identification (PI) bounds in causal inference by incorporating covariate information through a conditional optimal transport (COT) framework. The authors propose a novel relaxation that reduces COT to standard optimal transport (OT), improving computational feasibility while maintaining the benefits of covariate adjustment. The approach enables a data-driven estimation of the PI set using existing OT solvers. Theoretical analysis includes convergence guarantees and an exploration of asymptotic properties. Empirical validation is performed using synthetic and real-world data, demonstrating superior performance over existing methods in terms of bound tightening and estimation accuracy.
Claims And Evidence: All the claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed method is able to estimate partial identification bound with covariate adjustment.
Theoretical Claims: The theoretical claims seem correct.
Experimental Designs Or Analyses: NA
Supplementary Material: NA
Relation To Broader Scientific Literature: NA
Essential References Not Discussed: NA
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We highly appreciate the positive comments of the reviewer and are happy to answer any question if needed. | Summary: This paper leverages the conditional optimal transport (COT) to derive or tighten the partial identification (PI) bounds for some causal estimands. Since the COT is not easy to compute in practice, the authors propose a relaxation based on mirror covariates, leading to a optimization problem whose objective function interpolates between the unconditional and conditional optimal transport problems for the PI bounds. The convergence properties of the plug-in estimator are also studied. Finally, the authors also compare their estimator with the existing one that also utilizes the optimal transport technique.
Claims And Evidence: All the claims and theory in this paper are clear and supported by rigorous proofs or empirical experiments.
Methods And Evaluation Criteria: The proposed methods for using the conditional optimal transport on the partial identification bounds make sense to me. In addition, the simulation studies and experiments are illuminating.
I only have concerns on a minor point: for Assumption 3.3, why is it important to assume that $\nabla_y h(y,\cdot)$ is injective for all $y\in \mathcal{Y}$? Are there any example causal estimands where this Assumption does not hold?
Theoretical Claims: Yes, I basically checked all the proofs for the theoretical claims in this paper. All of them are rigorous and clear.
There is only a minor question on Proposition 4.1 and its proof: as $n,m\to\infty$, do we need the ratio $\frac{n}{m}$ to converge to a positive constant? If $\frac{n}{m}\to 0$ or $\frac{n}{m}\to \infty$ as $n,m\to\infty$, it might not affect the consistency but I suspect that it will affect the convergence rate.
Experimental Designs Or Analyses: Yes, I checked all the experimental designs and analyses carefully. The results are solid. However, I have a question or comment on Table 3 that the authors may consider: Can the authors somehow obtain the true value of $\rho$ in this example? If not, I would suggest running some simulation where the authors know how to compute the true $\rho$. Then, suppose that $\rho \in (0,1)$ and the proposed estimator is applied on the data to compute the lower bounds for $\rho$. As $\eta$ grows, we would expect that the lower bounds are bigger than 0 as well. In this case, the partial identification lower bounds are meaningful.
Supplementary Material: Yes, I basically checked the entire supplementary material. The proofs are solid, and the writings are clear. A small suggestion is on Line 756: given that Theorem 10.28 in Villani et al. (2009) has been used multiple times with several different conditions, I believe it would be better to restate this theorem as a Lemma in the appendix.
Relation To Broader Scientific Literature: This paper improves upon a paper by Ji et al. (2023) by utilizing the techniques related to conditional optimal transport.
Ji, W., Lei, L., and Spector, A. Model-agnostic covariate-assisted inference on partially identified causal effects. arXiv preprint arXiv:2310.08115, 2023.
Essential References Not Discussed: Not that I am aware of. However, for the contents between Lines 639 and 646, it seems that the discussions are duplicated.
Other Strengths And Weaknesses: One important point that the author may consider addressing is to design a valid statistical inference procedure on the partial identification bounds. This can help further advance the impacts of this paper.
Other Comments Or Suggestions: 1. For the description of Figure 1, it would be clearer to state that $P(Z=1)=P(Z=0)=\frac{1}{2}$.
2. Second column of Line 217: Can the authors generalize the results to convex cost functions?
3. Second column of Line 231: a typo "certein" should be "certain".
4. For Figures 3 and 4, since the authors did Monte Carlo experiments, it would be better to plot the standard error of each curve in the plots as shared regions as well.
5. For Figure 3 (c,f), I wonder why the $L_1$ error of $\hat{V}_{ip}(\eta)$ will eventually go up as $\eta$ increases.
6. On Line 727: did you define the operation $\circ$ somewhere in the paper?
Questions For Authors: See my comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We greatly appreciate the reviewer's summary and questions. In the following, we address each question individually.
> In Assp 3.3, why is it important to assume that $\nabla_y h(y, \cdot)$ is injective for all $y \in \mathcal{Y}$ ?
This is because we define the $V_{ip}(\eta)$ by the expectation of $h$ under a coupling $\pi$ that is computed through our mirror-relaxed OT problem. To make the $\pi$ well-defined, a standard assumption of to let the objective to have an injective gradient everywhere, e.g., a quadratic function.
> In Prop 4.1, do we need the ratio $\frac{n}{m}$ to converge to a positive constant?
For Prop 4.1, as long as $m,n \rightarrow \infty$, the estimator is consistent. The convergence rate may depend on the ratio $\frac{n}{m}$, but we do not invetigate in this direction. Alternatively, in Thm 4.1, we let the convergence rate to depend on $\min (m,n)$.
> For Table 3, can the authors somehow obtain the true value of $\rho$ in this example?
Unfortunately, in table 3, we are analyzing a real dataset and the true value of $\rho$ is unidentifiable. We thank the reviewer for their suggestion on making a simulation such that $\rho > 0$ and the lower bound is meaningful. As a response to this, we can actually twist the synthetic experiments in Fig 3 to set the estimand to be $\rho > 0$, since estimating $\rho$ is essentially estimating for quadratic $h$. In the real dataset, the sample appears to be noisy and the correlation between covariate and outcome is not as significant as that in the synthetic dataset (this is why the lower bound is negative, indicating that we cannot reject the possibility of negative $\rho$); In Fig 3, we have larger sample, the estimation error is relatively small, and we set the correlation to be significantly positive, therefore, in that case, the lower bound will be larger than zero.
> One important point that the author may consider addressing is to design a valid statistical inference procedure on the partial identification bounds.
The OT estimation may struggle when the dimension of covaraite plus outcome is larger than three, thus a useful inference procedure would be challanging to construct. However, when the dimension is smaller than three, there are some CLT limiting results that can be used to build an inference procedure. We will leave this for future research.
> Can the authors generalize the results to convex cost functions?
This is also in our scope of the future research. In the present version, the results depends on the convergence rate of the Brenier's map, which are studied under quadratic loss function. An extension to convex cost functions would be very nontrivial, and we are investigating alternative ways to reduce the effect of large $\eta$ on the magnitude of the estimator.
> For Figure 3 (c,f), I wonder why the $L_1$ error of $\hat V_{ip}(\eta)$ will eventually go up as $\eta$ increases.
This is because even though $V_{ip}(\eta) \leq V_{c}$ in the population level, the estimator $\hat V_{ip}(\eta)$ may overestimate $V_{ip}(\eta)$ to be larger than $V_{c}$ based on a finite sample. Therefore, for the $\eta$ such that $\hat V_{ip}(\eta)$ is larger than $V_{c}$, the $L_1$ error increases since $\hat V_{ip}(\eta)$ is increasing with respect to $\eta$.
> On Line 727: did you define the operation $\circ$ somewhere in the paper?
Sorry for the confusion, $\circ$ denotes the composition of mapping, which will be added in the revised version. | Summary: This paper studies partial identification intervals for the Rubin causal model, which is an important problem in the causal inference literature. The problem arises from the fact that we can never observe the counterfactual. Indeed, while the treatment effect (obtained when choosing h(Y(1), Y(0)) = Y(1) - Y(0) ) is still identifiable, the expected term E h(Y(1), Y(0)) is generally not identifiable for general choices of h.
Nevertheless, we can find lower bounds for this term. Two natural lower bounds have been discussed in the literature. 1) the optimal lower bound that requires to solve a conditional OT problem, and 2) a strong relaxation where we ignore the dependency on the covariates Z, resulting in an OT problem. This paper proposes a very elegant approach for improving upon 2) while still only relying on the solution of a normal OT problem and not of a conditional OT problem.
The problem is relevant and the paper is well written and very well executed. I recommend the acceptance of the paper. To support an award such as a spotlight or oral presentation, I would however expect a stronger motivation for the broader impact of this paper.
Claims And Evidence: Yes, all claims are well supported.
Methods And Evaluation Criteria: Yes, the paper evaluates their method on both synthetic data as well as real world data.
Theoretical Claims: The paper provides an informative finite sample analysis in Section 4. I have not checked the proofs in depth, but the results match expected rates and the proofs are well written and organised.
Experimental Designs Or Analyses: The experimental design is well executed.
Supplementary Material: I partially read the supplementary material, however not in detail. The appendix is well organised and decently well polished.
Relation To Broader Scientific Literature: I have published in the causal inference domain.
Essential References Not Discussed: I think the authors do a good job in discussing the literature.
Other Strengths And Weaknesses: -
Other Comments Or Suggestions: I think this is a nice paper and the authors found a good balance between theory and experimental results. I don't know of any suggestion that would strictly improve the current document.
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We highly appreciate the positive comments of the reviewer and are happy to answer any questions if needed. | Summary: This paper tackles the challenge of partial identification (PI) in causal inference, where causal estimands depending on the joint distribution of potential outcomes are not fully identifiable. While incorporating covariate information can tighten PI bounds, solving the corresponding Conditional Optimal Transport (COT) problem is computationally demanding and statistically unstable. The authors propose a **mirror relaxation** of COT that transforms it into a standard Optimal Transport (OT) problem with an added penalty term encouraging covariate consistency. This approach—termed **interpolating OT (Vip(η))**—creates a family of bounds interpolating between unconditional OT (Vu) and exact COT (Vc). The paper proves that the bounds become tighter with larger penalty, and the approach is consistent, computationally tractable, and robust. Theoretical results include convergence rates and interpolation properties. Experiments on synthetic and real data (including the STAR dataset) demonstrate improved performance over existing COT-based methods in both accuracy and efficiency.
## Update after the rebuttal:
Thanks for your response. It is an interesting topic. However, I have consistently regarded this work as a brief extension of the paper[1] by additionally incorporating covariate elements into the analysis. This addition does not appear to increase the technical complexity. A more precise explanation from the authors regarding the core technical challenges of this work, as compared to prior literature, would be instrumental in convincing me of the paper's contributions. Besides, the experimental part is also weak.
Thanks for your response. I increase my score to 3.
[1] Bridging multiple worlds: multi-marginal optimal transport for causal partial-identification problem, Zijun Gao, Shu Ge, Jian Qian
Claims And Evidence: The paper claims:
- A novel relaxation of COT leads to computationally efficient and statistically consistent PI estimation.
- The proposed interpolated bounds (Vip(η)) tighten PI intervals compared to unconditional OT, and converge to exact COT as η → ∞.
- The method achieves improved empirical performance in both synthetic and real-world settings.
These claims are well-supported by:
- Rigorous theoretical development, including interpolation guarantees (Proposition 3.6) and finite-sample convergence bounds (Theorem 4.3).
- Extensive synthetic experiments comparing their method to DualBounds, with results showing tighter intervals and more accurate estimates.
- Real data application demonstrating narrower confidence intervals and better correlation estimation than baselines.
Methods And Evaluation Criteria: The method is mathematically elegant and well-motivated:
- The use of mirror covariates enables re-formulating COT into a penalty-regularized OT problem.
- The Vip(η) formulation interpolates smoothly between OT and COT bounds.
- The estimator is simple to implement using standard OT solvers (e.g. Sinkhorn, LP).
Evaluation is comprehensive:
- Includes both synthetic setups (with known ground truth) and real-world datasets.
- Comparison with DualBounds under various model types (linear, quadratic, scale) and nuisance estimators (ridge, KNN).
Theoretical Claims: The paper provides strong theoretical contributions:
- Interpolation result (Proposition 3.6) establishes that Vip(η) bridges Vu and Vc.
- Theorem 4.3 shows convergence rates under quadratic costs using Brenier maps and convexity theory.
- Extensions to α-mixing and non-i.i.d. settings (Theorem 4.7) are thoughtful and relevant.
Assumptions (smoothness, compact support) are clearly stated and reasonable in causal inference contexts.
Experimental Designs Or Analyses: Experiments are well-designed:
- Synthetic data covers three structural models (linear, quadratic, scale), highlighting method robustness.
- Real data (STAR dataset) shows practical impact by tightening Neyman variance bounds and PI on correlation.
- Metrics are interpretable (e.g., PI length, L1 error to oracle, variance estimator, sample size equivalence).
- Use of existing baselines (DualBounds) provides fair comparison.
Plots and tables clearly support conclusions.
Supplementary Material: The appendices include:
- Full theoretical proofs (existence, uniqueness, interpolation, convergence)
- Details of OT solvers used
- Gaussian examples with closed-form analysis
- Discussion of Brenier potential curvature bounds and implications
- Related work survey (copulas, COT, causal OT)
These supplements are rigorous and enhance the technical depth and clarity of the main paper.
Relation To Broader Scientific Literature: The paper makes a novel contribution at the intersection of optimal transport and causal inference:
- It builds on prior work on partial identification (e.g., Ji et al., 2023; Chemseddine et al., 2024) and causal OT.
- It sidesteps the estimation pitfalls of COT by introducing a penalty-based relaxation grounded in OT theory.
- The authors relate their method to copula bounds, GAN-based OT, and convex transport maps, integrating multiple threads of literature.
Essential References Not Discussed: No essential omissions were identified. The paper discusses both econometric and ML-focused OT methods, and thoroughly compares with relevant baselines (e.g., DualBounds). Related work on copulas, semi-parametric bounds, and Brenier-based methods are well-cited.
Other Strengths And Weaknesses: **Strengths:**
- Elegant theoretical formulation with interpolation between known extremes.
- Statistically grounded and computationally feasible.
- Strong empirical performance, including on real data.
- Avoids reliance on unstable nuisance estimation.
**Weaknesses:**
- The penalty parameter η still requires tuning.
- No analysis of worst-case efficiency loss relative to true COT.
- Extension to multi-valued or continuous treatments is not discussed.
Other Comments Or Suggestions: NA
Questions For Authors: 1. **Penalty Parameter Selection (η):**
Your method critically depends on the penalty parameter η for interpolation between Vu and Vc. However, no practical strategy is provided for choosing η. Can you suggest a data-driven or theoretically justified selection method (e.g., minimizing empirical PI width with statistical guarantees)? What are the consequences of over- or under-penalizing?
2. **Efficiency Loss Compared to COT:**
While you prove that Vip(η) interpolates between Vu and Vc, you do not quantify how close Vip(η) is to Vc in practice. Can you provide theoretical bounds (e.g., in terms of η, dimension, sample size) or empirical results that quantify the potential efficiency loss?
3. **Scalability to High Dimensions:**
OT-based methods are known to struggle in high-dimensional spaces. Have you evaluated how your method behaves as the dimension of covariates (Z) increases, particularly in terms of sample complexity and computation?
4. **Tuning η vs. Overfitting in Finite Samples:**
Since η indirectly governs the extent of covariate adjustment, can tuning it on the same sample introduce overfitting (e.g., inadvertently fitting to noise)? How robust is your plug-in estimator to this issue?
5. **Extension to Multi-valued or Continuous Treatments:**
Your framework is based on binary treatment. Can the mirror-relaxation idea extend to multi-valued or continuous treatments? If not directly, what conceptual or computational barriers would arise?
6. **Sensitivity to Misspecified Cost Function (h):**
Your theoretical results assume a known and fixed cost function. In practice, h may itself be misspecified or learned from data. How sensitive is your approach to the choice or error in h?
7. **Real-World Deployment and Interpretability:**
In applied domains (e.g., medicine, economics), interpretability and ease of use are key. Can you comment on how practitioners should interpret the Vip(η) bounds, and whether the required penalization intuition is accessible to non-theorists?
8. **Comparison to Semi-Parametric Bounds (e.g., Fan et al., 2023):**
How does your method compare (in tightness or assumptions) to other approaches that derive bounds using semi-parametric methods or variance inequalities? Can the two be combined?
9. **Alternative Relaxations Besides Mirror Covariates:**
Mirror covariates are introduced as a practical workaround to COT. Did you explore or benchmark other forms of COT relaxations (e.g., entropic regularization, conditional adversarial OT)? Why is your choice preferable?
10. **Potential for Variable Selection:**
In the discussion, you mention future directions for covariate selection. Could your current framework be extended to perform automatic covariate selection (e.g., via L1 regularization or adaptive penalization)?
11. **Stability under Data Perturbations:**
Have you examined how stable the Vip(η) estimator is to data perturbations (e.g., small changes in treatment assignment or outcome)? Robustness to noise is important for PI estimation in observational data.
12. **Robustness to Hidden Confounding:**
Your results assume unconfoundedness (or randomization). In practice, hidden confounding is inevitable. Can the method be adapted or extended to provide valid bounds under partial confounding assumptions (e.g., Rosenbaum sensitivity models)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We address potential limitations.
> The penalty tuning.
We provide a data-driven selection method for Q1, which works well in Fig 3, 4.
> Efficiency loss relative to COT.
No direct estimator of COT has been established (see Q2). Although there is a gap of Vip and Vc, we maintain consistency and explicit convergence rate based on a finite sample, which is not known for COT.
> Multi-valued or continuous treatments.
Vip can be extended to multi-valued treatment using multi-marginal OT.
Continuous treatments are not applicable directly for classic OT framework.
> 1. Penalty:
Under-penalizing may get an estimator to be below the COT value. Over-penalizing leads to a slow convergence on the $\eta$ in Thm 4.3, (thus minimizing empirical PI width is not ideal). Notably, $V_{ip}(\eta)$ with arbitrary $\eta$ already improves over Vu by using covariate, Vc has no known direct estimator.
We use the elbow method to select $\eta$ as in [6], which is common in unsupervised setups, such as determining the number of principal components in PCA.
> 2. Loss to COT:
Exp 3.8 shows the gap between $Vip(\eta)$ and Vc for Gaussian model. In general, we do not have a bound. In Sec 6, we discuss a variant to address this issue.
We aim to utilize the covariate to improve over Vu. (Prop. 3.6, Sec 5). COT has no direct estimator, Vip possesses an explicit finite-sample convergence rate (Thm 4.3).
> 3. High Dim:
The convergence of OT value is known to depend on the dimension, like a rate of $O(n^{-2/d})$ for squared Wasserstein [7], which is sharp [4]. Note that, our convergence rate in Thm 4.3 is aligned with this result.
If we have a reliable parametric distribution of Y given Z, the Vip estimator is compatible with the models. But we should note the risk of model misspecification as in Fig 3. (b) (e).
If no parametric model is available, a variable selection method for covariate would help. See Q10.
> 4. Overfitting:
Fig 3 and Fig 4 show that the elbow method is stable as the sample size goes from 500 to 1500.
> 5. Extension:
For multi-level, the Vip estimator can be directly extended using the multi-marginal OT [5].
For continuous value, our causal bound is out of the scope of a standard OT framework.
> 6. Sensitivity to h:
The cost function h in the causal estimand is typically chosen by the user, e.g. Sec 5.3. The Vc is a minimum of a linear functional of h, an error of order $O(a)$ will cause an error of order at most $O(a)$.
> 7. Real-World:
Vip is the OT problem with objective h with encouraging the alignment of Z in the two groups by regularization. Regularization is popular in classic statistics and machine learning approaches, e.g. LASSO.
> 8. Semi-Parametric
Semi-para estimates identifiable causal quantities but we do partially identified ones.
Bounds based on variance inequalities are not consistent but ours is consistent.
Fan (2023) considers inference for PI with moment equalities.
They model the joint distribution of Y using copula, which is suited for univariate outcomes, but our approach can handle vectors. They use Bernstein copulas, but we have no restrictions on the coupling.
They require estimating conditional CDFs, we don’t.
> 9. Alters:
E.g. [3]. But our mirror method has pros: (i) the mirror relaxation $\leq$ COT, and for causal bound, an underestimation beats overestimation since a lower bound still forms a valid causal bound. (ii) we guarantee an improvement over Vu.
> 10. Var-Select:
$
\sup_{\eta} \inf_{\pi} \int h(Y(0), Y(1)) + \sum_{i} \eta_i |Z^{(i)}(0) - Z^{(i)}(1)| d\pi - C \sum_{i} |\eta_i|.
$
We use the L1 norm of the $\eta$ vector to encourage sparsity.
> 11. Data Perturb:
The robustness property of $V_{\ip}$ against data perturbation inherits from the stability of the OT with respect to its marginals. When the objective function $h$ is Lipschitz, then a distributional shift of order $O(a)$ measured in 1-Wasserstein distance induces a bias of at most order $O(a^{2/15})$ on the OT map used in computing $Vip(\eta)$, also the estimator [8].
> 12. Hidden Confound:
In this case, we can relax the OT. Suppose that the bias of observed conditionsal law is measured by a distance D and smaller than a constant, then a relaxed OT problem (or robust OT) can be used [1,2].
[1] "Optimal transport with relaxed marginal constraints."
[2] "On robust optimal transport: Computational complexity and barycenter computation."
[3] "Consistent optimal transport with empirical conditional measures."
[4] "Sharp convergence rates for empirical optimal transport with smooth costs."
[5] "Bridging multiple worlds: multi-marginal optimal transport for causal partial-identification problem."
[6] “Determining the number of clusters/segments in hierarchical clustering/segmentation algorithms.”
[7] “On the rate of convergence in Wasserstein distance of the empirical measure."
[8] "Quantitative stability of optimal transport maps and linearization of the 2-Wasserstein space." | null | null | null | null |
ALS: Attentive Long-Short-Range Message Passing | Reject | Summary: The paper presents Attentive Long-Short-range Message Passing to handle long-range dependencies while avoiding excessive memory usage and the over-smoothing problem
Claims And Evidence: The authors conduct extensive experiments on 14 datasets, covering homophilic, heterophilic, and long-range graph benchmarks. In addition, they compare their method with recent algorithms such as GAT, APPNP, and IGNN. Lastly, the ablation studies show the impact of key components, including DPPR, attention mechanisms, and acceleration techniques
Methods And Evaluation Criteria: The paper uses following metrics for evaluation: accuracy and F1 scores
Theoretical Claims: There seem to be no issues with the theoretical claims
Experimental Designs Or Analyses: The experiments cover diverse scenarios including homophily and heterophily. In addition, memory efficiency and training time are empirically validated
Supplementary Material: N/A
Relation To Broader Scientific Literature: The proposed PPR and disjoint message-passing are widely used in literature
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths
* The acceleration technique reduces computation time by up to 89.51%
* ALS is compared against well-established GNN models such as GAT, APPNP, and IGNN
* Soundness of experimental designs, where the chosen datasets (e.g., Amazon, OGB, COCO-SP) are widely used in GNN research
Weaknesses
* The novelty of this paper lies in the Differentiable Personalized PageRank (DPPR) and accelerated training. However, computing only the non-zero gradients of PPR (Theorem 3.1) was already proposed in [1] (page 5, Section B). Additionally, the contribution of long-short-range message passing is incremental, as it was introduced in [2]. While long-short-range message passing may be effective for both homophilic and heterophilic graphs, the proposed algorithm is merely a simple integration of several existing methods, which significantly limits its novelty
* [1]: Efficient Algorithms for Personalized PageRank Computation: A Survey
* [2]: Long-short-range message-passing: A physics-informed framework to capture non-local interaction for scalable molecular dynamics simulation
* It would be better to demonstrate the effectiveness of the proposed method on widely used homophilic datasets (Cora, Citeseer, PubMed) and heterophilic datasets (Actor, Chameleon, Squirrel)
Other Comments Or Suggestions: N/A
Questions For Authors: Could you elaborate on the above weaknesses?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: ## Response to concerns regarding novelty
We have carefully examined the references you kindly pointed out and would like to clarify several aspects:
> computing only the non-zero gradients of PPR (Theorem 3.1) was already proposed in [1]
We respectfully note that the computation of non-zeros in $A \odot (\nabla_Z \cdot Z^T)$ at line 215 is not included in Theorem 3.1.
So **even if** similar gradient computation methods exist, this does not diminish the novelty of Theorem 3.1, which demonstrates how to optimize a PPR process iterated to convergence - a fundamentally different approach from existing PPR-based methods with truncated iterations (e.g., PPNP and MAGNA).
Moreover, the non-zero computation you mentioned in [1] actually refers to computing $P \hat \pi_s^{(L)}$.
It is simply a forward-pass propagation, analogous to computing $A X$ in our framework.
This differs significantly from our edge-wise computation of $A \odot (\nabla_Z \cdot Z^T)$.
> "the contribution of long-short-range message passing is incremental"
We are afraid that the reference [2] shares only method name similarity with our approach.
Their method addresses molecular dynamics simulation in a two-level graph structure (atom-level many-body interations and molecule-level long-range interactions), whereas our work focuses on single-graph learning with distance-aware message passing.
And heterophily is not considered in [2].
> "the proposed algorithm is merely a simple integration of several existing methods"
Due to the previous explanations, **we respectfully disagree with your assessment.**
However, we greatly appreciate your positive comments on other aspects of our work.
* [1] Efficient Algorithms for Personalized PageRank Computation: A Survey
* [2] Long-short-range message-passing: A physics-informed framework to capture non-local interaction for scalable molecular dynamics simulation
## Response to concerns on datasets
We sincerely appreciate your suggestion to evaluate ALS on additional datasets.
However, we would like to note that reference [3] identifies significant limitations with Cora, Citeseer and Pubmed datasets, particularly regarding fragile and misleading results from their data splits.
These datasets also represent a narrow range of network types (all citation networks).
We instead employ the Amazon Computer, Amazon Photo, Coauthor CS, and Coauthor Physics datasets recommended by [3] as more robust homophilic benchmarks.
For heterophilic graphs, reference [4] demonstrates issues with traditional datasets (e.g., train-test leakage in Chameleon and Squirrel) and proposes new benchmarks - the five heterophilic datasets we adopted.
While we would be happy to conduct additional evaluations on your suggested datasets, we believe our current selection better represents modern, rigorous benchmarking practices in graph learning research.
* [3] Shchur O. Pitfalls of Graph Neural Network Evaluation. ArXiv 2018 (#Citation: 1620)
* [4] Platonov O. A critical look at the evaluation of GNNs under heterophily: Are we really making progress? ICLR 2023 | Summary: Overall, the core contribution of ALS includes a differentiable personalized PageRank and a short-range message-passing module for effectiveness and efficiency consideration of graph deep learning. The experiments are extensive, and the results are competitive. The writing and the organization of the paper can be largely improved, some critical parts are not quite clear. Details are as follows.
Claims And Evidence: Most claims are supported. Two major concerns are listed below.
1. In the abstract and introduction, oversmoothing is regarded as one of the motivations of the paper. It is not easy to trace the relation between oversmoothing and the proposed method and how it can alleviate this problem theoretically and empirically.
2. The derivation or proof of theoretical time complexity mentioned in the abstract is not easy to locate in the main body of the paper.
Methods And Evaluation Criteria: Evaluation criteria are fair and reasonable.
Theoretical Claims: As mentioned above, the detailed derivation of theoretical analysis seems missing.
Experimental Designs Or Analyses: Overall, the performance of the proposed method seems competitive.
In table 1, "baselines" are vague.
Supplementary Material: I reviewed the entire supplementary material.
Relation To Broader Scientific Literature: Graph deep learning framework is interesting and important to many real-world impactful applications. The scope and vision of the paper is good.
Essential References Not Discussed: To the best of the reviewer's knowledge, there is no big problem in this part.
Other Strengths And Weaknesses: Additional weaknesses:
1. In Section 3.1, the theorem comes as a sudden, very limited formation or expression of DPPR is introduced before, which makes it very hard to follow. It would be better to give the formal definition and expression of DPPR before the theoretical analysis.
2. The Equation (1) seems problematic, the dimension is inconsistent. $\mathbf{X}$ is $\mathbb{R}^{n \times d}$, but $\mathbf{Z}$ seems to be $\mathbb{R}^{n \times c}$, where $d$ is the number of input features, and $c$ is the number of labels, no matter based on line 124 in the paper or the original APPNP paper.
3. [Optional] Baselines in Table 4 are a subset of the mentioned in Section 4.3, and Section 4.3 lacks the baselines after 2023.
Other Comments Or Suggestions: Please see all above
Questions For Authors: Please see all above
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's time and valuable feedback.
We hope our following clarifications help the reviewer better appreciate the significance of our contributions, and we would be happy to provide any additional information that might assist in their evaluation.
## Oversmoothing
> It is not easy to trace the relation between oversmoothing and the proposed method
We sincerely appreciate this thoughtful observation regarding oversmoothing analysis.
As demonstrated in prior work [1,2], the integration of Personalized PageRank (PPR) fundamentally addresses oversmoothing in graph neural networks.
Since this relationship has been well-established in the literature, we did not show the alleviation of this problem in our manuscript but focused our experimental validation on the novel aspects of our approach.
* [1] Klicpera J. Predict then Propagate: Combining neural networks with personalized pagerank for classification on graphs. ICLR, 2018
* [2] Choi J. Personalized pagerank graph attention networks. ICASSP, 2022
## Complexity
> The derivation or proof of theoretical time complexity mentioned in the abstract is not easy to locate
We appreciate this careful reading.
We would like to clarify that the complexity analysis mentioned in the abstract specifically refers to memory complexity rather than time complexity.
We will ensure this distinction is made clearer in any subsequent revisions.
## Baselines
> In table 1, "baselines" are vague.
Thank you for this helpful feedback.
Table 1 presents aggregated results comparing our method against all baselines.
The "Rank-1" column indicates the highest-performing baseline result for each dataset, while "Rank-2" shows the second-best baseline performance.
Complete baseline results are available in Appendix E for reference.
> Baselines in Table 4 are a subset of the mentioned in Section 4.3
Thank you for this observation.
We have verified that baselines are correctly described.
The second paragraph of Section 4.3 describes baselines for Table 1, which is the combination of Table 4 and Table 5.
In those baselines, only LINKX does not show up in Table 4, but it is in Table 5.
The third paragraph introduces baselines for Table 2.
So these baselines does not have to show up in Table 4.
> Section 4.3 lacks the baselines after 2023
We appreciate this suggestion for contemporary comparisons.
Our evaluation includes several recent works of 2024, namely Graph Mambas [3,4].
While other baselines predate 2023, many of them are from the recent literature [5].
* [3] Behrouz A. Graph mamba: Towards learning on graphs with state space models. KDD 2024
* [4] Wang C. Graph-mamba: Towards long-range graph sequence modeling with selective state spaces. arXiv 2024
* [5] Chenhui D. Polynormer: Polynomial-Expressive Graph Transformer in Linear Time. ICLR 2024
## Notations
> In Section 3.1, the theorem comes as a sudden...
We apologize for any confusion caused by the theorem's presentation.
The notation PPR($\alpha$, A, X) is explicitly defined in line 117 of the manuscript.
We will consider adding additional transitional text to improve the flow in future revisions.
> The Equation (1) seems problematic, the dimension is inconsistent...
We appreciate this careful examination of our equations.
The dimensions are indeed consistent: $x_i \in \mathbb{R}^{1 \times d}$ (line 89), so $q_i, k_j \in \mathbb{R}^{1 \times c}$ and $s_{ij}$ is a scalar.
$c$ is just another dimension, not the number of labels.
$\mathbf{Z}$ is node representations (same dimensionality as $\mathbf{X} \in \mathbb{R}^{n \times d}$) rather than classification outputs. | Summary: This study introduces Attentive Long-Short-range message passing (ALS), which combines personalized PageRank to address over-smoothing and utilizes GAT for capturing complex data dependencies, significantly reducing memory footprint and computation time. Extensive experiments show that ALS achieves competitive or superior results compared to other baselines.
Claims And Evidence: It is easy to follow. However, while the authors claim that the proposed method mitigates oversmoothing, the experimental results do not provide a detailed analysis. Moreover, the results in some cases do not show significant improvement over existing methods, and additional experiments or clearer explanations are needed.
Methods And Evaluation Criteria: The method primarily comprises three components: differentiating the Personalized PageRank (PPR) process, employing techniques to accelerate PPR, and integrating a short-range message passing module. Extensive experiments on multiple datasets are conducted to evaluate the effectiveness of the proposed method.
Theoretical Claims: The theory demonstrates the availability of differentiable Personalized PageRank (PPR).
Experimental Designs Or Analyses: 1. While the algorithm's complexity is analyzed, it would be beneficial to also evaluate its memory usage with other baselines.
2. Although the proposed method is designed to capture long-range information, it does not achieve significant improvements on two datasets with long-range dependencies.
Supplementary Material: Appendix E.
Relation To Broader Scientific Literature: It contributes to GNN.
Essential References Not Discussed: No
Other Strengths And Weaknesses: No
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: ## Oversmoothing
> While the authors claim that the proposed method mitigates oversmoothing, the experimental results do not provide a detailed analysis.
We appreciate this observation regarding oversmoothing.
As established in prior work [1,2], the incorporation of Personalized PageRank (PPR) inherently addresses the oversmoothing issue in graph neural networks.
Since this has been thoroughly demonstrated in the literature, we did not show the mitigation of oversmoothing in our manuscript but focused our experimental validation on other novel aspects of our approach.
* [1] Klicpera J, et al. Predict then Propagate: Combining neural networks with personalized pagerank for classification on graphs. ICLR, 2018
* [2] Choi J. Personalized pagerank graph attention networks[C]. ICASSP, 2022.
## Are improvements significant?
> Results in some cases do not show significant improvement over existing methods, and additional experiments or clearer explanations are needed.
We respectfully submit that improvements exceeding one standard deviation in accuracy can reasonably be considered significant.
Our method achieves this standard in 9 out of 12 datasets in Table 1 and demonstrates consistent significance when compared to MPNN baselines in Table 2.
While we understand the desire for universal improvement across all cases, we believe this may be an overly stringent expectation given the diversity of graph datasets.
To better address the reviewer's concern, we would be grateful for more specific guidance regarding what 'additional experiments or clearer explanations' would be most valuable for evaluating our method's contributions.
## The memory usage
> While the algorithm's complexity is analyzed, it would be beneficial to also evaluate its memory usage with other baselines.
We appreciate this suggestion regarding memory analysis.
The attention weights of ALS are computed with the same formula in standard GAT.
The difference is that ALS will propagate information following these attention weights for multiple iterations.
However, the memory usage maintains the same thanks to implicit differentiation, as shown in Figure 2.
Thus, the memory usage of ALS is the same as GAT.
## Are improvements significant with long-range dependencies?
> Although the proposed method is designed to capture long-range information, it does not achieve significant improvements on two datasets with long-range dependencies.
This is an insightful observation.
We agree that when compared to Graph Transformers (GT), ALS shows more modest improvements because GTs inherently possess global receptive fields that can capture both long-range and non-adjacent node dependencies.
However, as an MPNN variant, ALS consistently outperforms other MPNN baselines by more than one standard deviation in accuracy.
Furthermore, the integration of ALS with GT architectures yields better performance than other MPNN-GT combinations.
These results substantiate our claim that ALS offers superior long-range information capturing capability compared to conventional MPNN approaches. | Summary: This study introduces Attentive Long-Short-range (ALS) message passing, which incorporates personalized PageRank to address the over-smoothing issue in long-range message propagation. Additionally, it utilizes implicit differentiation to effectively improve the GAT computation overhead.
Claims And Evidence: While the study presents experiments demonstrating the performance of ALS across various graph types, its scope is limited to evaluating effectiveness in the node classification setting. This narrow focus raises concerns about the method’s generalizability to other graph-related tasks, such as link prediction or graph classification. Additionally, while ALS is compared against strong baselines like Graph Transformers and Graph Mambas, the study lacks a thorough analysis of computational efficiency and scalability.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria are appropriate for the problem at hand. However, the study lacks an analysis of the method’s generalizability to other graph-related tasks, such as link prediction or graph classification, limiting its broader applicability.
Theoretical Claims: I have checked the proofs and noted that the paper includes only one theorem. However, I find the authors' claim of proposing three acceleration techniques for expediting the computation of Differentiable PPR to be unsubstantiated. The section lacks genuine innovation, as it merely employs existing optimization techniques rather than introducing novel computational advancements. A more rigorous justification or empirical demonstration of how these techniques specifically enhance Differentiable PPR would strengthen the contribution.
Experimental Designs Or Analyses: Detailed model settings are unavailable, making it difficult to reproduce the experimental results. Key details, such as the number of layers and hidden units used for ALS, are not clearly specified. Additionally, the study omits certain long-range graph benchmarks, which limits the comprehensiveness of the evaluation. Furthermore, there is no ablation study examining the effectiveness of different optimization techniques, leaving their individual contributions unclear.
Supplementary Material: Yes, the proof for the Theorem.
Relation To Broader Scientific Literature: Enhancing the performance of GNNs has implications for graph-based learning across multiple domains. This work leverages attention mechanisms to construct an attentive transition matrix for message passing, improving its ability to capture intricate data dependencies effectively.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The proposed method seems effective and performs well empirically.
The introduction of DPPR is an interesting idea.
The paper's structure is clear and easy to follow.
Other Comments Or Suggestions: n/a
Questions For Authors: In Figure 1, there is a discussion comparing single-layered ALS to multi-layered ALS. Could you clarify why stacking multiple ALS layers is helpful for the downstream performance? Any further explanation on this would be helpful.
Ethical Review Concerns: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: ## Link prediction and graph classification
> This narrow focus raises concerns about the method’s generalizability to other graph-related tasks, such as link prediction or graph classification.
> The study lacks an analysis of the method’s generalizability to other graph-related tasks.
We sincerely appreciate the reviewer's valuable suggestion regarding additional evaluation tasks.
Due to time constraints during the rebuttal period, we may not be able to conduct comprehensive evaluations across different types of graph tasks.
However, we would like to note that among the PPR-based methods we referenced (APPNP, GPRGNN, PPRGo, PPRGAT, and MAGNA), only MAGNA included link prediction evaluations.
Therefore, focusing on node classification for our DPPR-based ALS method aligns with standard practice in this research area.
Furthermore, all claims in our manuscript - including memory optimization, time efficiency, and effectiveness on heterophilic graphs - have been thoroughly validated.
Since heterophily fundamentally concerns node-level relationships, node classification tasks sufficiently demonstrate our method's capabilities in this regard.
## Efficiency and scalability
> the study lacks a thorough analysis of computational efficiency and scalability.
We acknowledge the reviewer's concern about computational analysis.
The attention weight computation in ALS follows the same algorithmic approach as standard GAT.
The key distinction lies in ALS's multiple iterations of information propagation, which typically results in computation time proportional to the number of iterations compared to GAT.
This iteration count is primarily determined by the parameter $\alpha$ and can be significantly reduced by our three acceleration techniques.
Regarding scalability, our experiments demonstrate ALS's scalability because they include two large-scale OGB datasets, and while individual subgraphs in the LRGB datasets are small, their combined scale is substantial.
## The innovation of accelerating techniques
> I find the authors' claim of proposing three acceleration techniques for expediting the computation of DPPR to be unsubstantiated.
We appreciate this opportunity to clarify our technical contributions.
As mentioned in our discussion of AdaTerm, traditional PPR applications typically solve a single linear system, whereas we must solve H × C independent linear systems due to the multi-dimensional nature of node representations in GNNs.
This novel challenge motivated our AdaTerm.
Moreover, the multi-dimensional node representations make Krylov subspace methods difficult to apply. While Krylov methods may require dozens of basis vectors to construct subspaces (negligible overhead for single systems), combining them with GNNs would require independent subspaces for each representation dimension, leading to H × C times of memory usage.
This inspired our SymGAT, which enables more memory-efficient conjugate gradient algorithms.
Regarding EigenInit, since PPR was originally designed for homophilic graphs like page recommendations where EigenInit showed limited benefits, traditional PPR methods did not investigate into it.
However, our experiments demonstrate that EigenInit provides significant acceleration on heterophilic graphs - an important finding given the growing interest in heterophilic graph research.
In summary, the three techniques were specifically designed to enhance PPR-based GNN methods, including our DPPR approach.
## Experimental Designs Or Analyses
We respectfully disagree with this particular critique.
We have provided detailed experimental settings in Appendix E and included reproduction scripts with submitted code.
We omit other LRGB datasets because they are inadequate for the evaluation, as explained in the footnote on page 6.
Furthermore, Appendices C and D contain extensive ablation studies - we believe these address the reviewer's concerns about 'different optimization techniques'.
We would welcome further clarification if we have misunderstood the reviewer's point.
## Multi-layered ALS
> why stacking multiple ALS layers is helpful?
This is an excellent and commonly raised question about many methods.
As shown in Appendix C of the IGNN paper, stacking multiple layers is theoretically equivalent to using a single wider layer.
However, empirical results demonstrate that multi-layer IGNN architectures achieve substantially better performance on datasets like PPI.
A similar phenomenon occurs with Graph Transformers (GT) - while a single GT layer can theoretically access all global information, deeper architectures typically perform better.
Our work validates this design pattern's effectiveness, though the underlying reasons remain an open research question.
We hope this common architectural consideration won't negatively impact the evaluation of our contributions. | null | null | null | null | null | null |
Generative Audio Language Modeling with Continuous-valued Tokens and Masked Next-Token Prediction | Accept (poster) | Summary: The paper proposes a text-to-audio model that leverages diffusion-based designs and causal language models, named AudioMNTP. In detail, the model applies a transformer-based decoder for the next-token prediction of the feature in latent space before being forwarded into the diffusion-based structure, then follows a VAE decoder and Gan-based vocoder to reconstruct the waveform. In addition, a token masking strategy is proposed to improve the model performance. Experiments illustrate that the proposed model achieves state-of-the-art performance with a significantly lower model size.
Claims And Evidence: The authors claim that previous diffusion-based audio language models present bottlenecks and limitations. However, evidence supporting the effectiveness and superiority of the proposed AudioMNTP models over simpler baselines is not adequately provided. A suggestion is to provide some demos to support such a claim and also present the enhancement by the proposed methods Additionally, the introduction of both the transformer-based decoder and the overall structure is not very understandable.
Methods And Evaluation Criteria: The proposed system mainly applies AudioCaps and WavCaps for training. However, the availability of upscaling the dataset with numerous other audio-language datasets remains unclear. Although the author claims that the upscale of the model is limited by the computational constraints, the model is trained using 104 V100 GPUs for 5 days, such resource is already enough for any large model. The author provides various evaluation matrices to illustrate and compare the performance, however, the result including speech and non-speech categories is hard to understand, Does this mean that the proposed model can correctly generate speech contents?
Theoretical Claims: All the theoretical claims are discussed in the paper, however, the written format of the paper could be improved, currently,y the structure is hard to follow and understand. Why does the paper actually provide the details of two models, AudioNTP and AudioMNTP? The introduction of the inference section for both models is also ambiguous. It is hard to understand how the decoder works during inference, is all the tokens are general noise in the beginning?
Experimental Designs Or Analyses: The paper lacks most of the essential details of the experiments, such as specific training/inference parameters of each model, e.g., the inference time. After reading the whole paper, it is still hard to understand the pipeline of the system and how the model actually operates.
Supplementary Material: As a generative model, the paper should provide demo audios to illustrate the performance of the system, especially the demos to compare the effectiveness of each proposed modules/strategies.
Relation To Broader Scientific Literature: The paper discusses a new idea of applying the advantage of causal language models for generative models. In addition, MAE-based training strategies are applied to improve performance.
Essential References Not Discussed: There are actually more text-to-audio models which have achieved better performance, such as AudioBox and Re-AudioLDM. Although it might be hard to run these models, the paper could be improved by discussing them.
Other Strengths And Weaknesses: The overall structure, especially the two graphs, is excessively complex and hard to understand or follow.
The format of the paper should also be improved, some sections are overlapped and the order of some parts should be improved.
The paper introduced many techniques but lacked the details of the proposed model. Currently, it is even unclear the overall pipeline of the model and how the transformer-based decoder with diffusion-head works.
The model did not provide any demos on the model.
Other Comments Or Suggestions: None
Questions For Authors: Overall, the model provides an enhanced performance with the smaller size of the system, however, the writing of the paper needs to be improved as the current file is hard to follow. I would be happy to increase the score if the author could answer the following questions and also explain the overall pipeline of the model.
Question 1:
What is the main proposed model, why introduce both AudioNTP and AudioMNTP? Are both necessary?
Question 2:
Why use MLP architecture for the diffusion-based section? Any consideration for other architectures?
Question 3
What is the overall structure of the model, is the proposed model mainly replacing the previous LDM/transformer-based feature generation model with the transformer-based decoder?
Question 4
Can we provide some demos of the result?
Question 5
What is the inference time of the proposed model?
Question 6
Why the evaluation in Table 2 being categorized into non-speech and speech, Does that mean the model can successfully generate real-speech content?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for the constructive feedback! Below, we address all comments and outline planned improvements.
---
# 1. Presentation Improvement
We agree the current version can be clearer and will revise structure, improve diagrams, and expand explanation in the final version.
> If you have specific instructions on the organization, please let us know!
#### **Relation between AudioNTP and AudioMNTP. Why show both AudioNTP and AudioMNTP? Are they both necessary? What is the final pipeline?**
AudioNTP introduces **continuous-valued tokens**, and AudioMNTP extends it with **MNTP** training. Both are our novel contributions, so introducing both is necessary. Table 1 shows both are key to achieving SOTA audio generation with LMs. AudioMNTP—integrating both—is our final proposal. For clarity, we illustrate the full AudioMNTP pipeline below, covering training and inference.
#### **Training**
> Please see [Figure A](https://imgur.com/XIsMoZB.png) for the training pipeline.
Waveforms are encoded into latents, masking is applied, and remaining tokens form a new sequence. A Transformer decoder performs next-token prediction on this masked sequence, guided by target positional embeddings. The LM outputs ($z$) go into a small MLP diffusion head, trained with diffusion loss to predict the next unmasked token.
> See our response to **Reviewer v7YS** for more on target positional embeddings.
#### **Inference**
> See [Figure B](https://imgur.com/RmptxLD.png) and [Figure C](https://imgur.com/aX2ivm4.png) for step-by-step inference.
Given the BOS token and text embedding, the model generates latent token $z^0$ using one Transformer pass. Conditioning on $z^0$, the audio token $x^0$ is sampled from noise via diffusion. Then $x^0$ is used to generate $x^1$ autoregressively. After generating a chunk of tokens, they are decoded into waveform using a VAE decoder and HiFi-GAN vocoder.
#### **Are all the tokens general noise in the beginning?**
Yes — each token is initialized with Gaussian noise and refined via the MLP diffusion head.
#### **Why use MLP for diffusion?**
A simple MLP keeps latency low and enables real-time generation, which current TTA diffusion models don’t support. If the diffusion head is too slow, denoising becomes a bottleneck. See our response to **Reviewer v7YS** for latency discussion.
#### **Does the model mainly replace LDMs with a Transformer?**
No. Our Transformer runs once per token to produce a conditioning input for the small MLP, which does iterative diffusion. LDMs run the full model at each diffusion step, causing high latency.
# 2. Does not compare to Diffusion-Based Audio LM Baselines
To our knowledge, this is the first use of continuous-valued tokens in LMs for TTA. If we missed related work, we’d appreciate pointers. The most [relevant work](https://openreview.net/pdf?id=y4LniyJIWi) cascade a discrete audio LM and a diffusion model, not a single diffusion-based audio LM. Also, it's not open-sourced.
We propose **AudioNTP** (the first diffusion-based Audio LM) and improve it with **AudioMNTP**. Table 1 compares our methods to LDMs and discrete LMs, supporting two key claims:
1. **Continuous audio LMs** outperform discrete ones.
2. **MNTP** improves training over next-token prediction.
# 3. Demos
Thanks for the suggestion! Please see our [demo page](https://audiomntp.github.io/). Our method outperforms AudioGen Large and AudioLDM2-Full-Large and matches Tango 2. Due to internal download limits, we can’t include more samples for the ablation. But Tables 3 & 4 support our claims.
# 4. Why not scale up the datasets?
Our method already achieves SOTA on standard datasets. We are scaling up and will include results in the final version if accepted (see reply to **Reviewer 8Ca7**). Thanks for the suggestion!
# 5. Why split into speech vs. non-speech?
Speech is harder to generate and not a common case in TTA. Most TTA systems — including ours — can’t generate intelligible speech. Since ~50% of AudioCaps involves speech, it can obscure performance on sound. So, we split evaluation into **pure sound** and **sound + speech** (see Appendix G). We agree current naming can be confusing and will revise them. The rationale will also be added to the main text.
# 6. Missing experimental details?
Most details are in Appendix F and G due to page limits. Let us know if anything should be moved to the main text or is missing.
# 7. AudioBox and Re-AudioLDM
These models are not public, so direct comparison is difficult. We will include discussion in the final version.
# 8. Inference time
Latency details will be added in the final version. Please see our response to **Reviewer v7YS** for results and discussion.
---
We appreciate your thoughtful feedback! Your comments helped us improve clarity and depth. If you feel your concerns are addressed, we’d be grateful if you could consider raising your score. Let us know if anything can be further improved. Thank you!
---
Rebuttal Comment 1.1:
Comment: Thanks for the reply from the author. However, I decided to keep the score as the author seems did not provide most of the requests(excluding the claim to be added to the final version).
---
Reply to Comment 1.1.1:
Comment: We thank the reviewer for the comments. However, we believe that we have addressed most of the reviewer's requests. For clarity, we summarize them point-by-point below:
# Main requests
---
### **Main Weakness: Presentation and Demo page**
We address the request in **"1. Presentation Improvement"**. Specifically, we provided 3 new figures and explanations to illustrate the training and inference pipeline step-by-step. Furthermore, we also mentioned the additional clarification on the target positional embedding in **"Response to Reviewer v7YS"**. Finally, we provided the demo page. We would be grateful if the reviewer could provide details on the reading difficulty so we can improve the organization!
### **Question 1: What is the main proposed model, why introduce both AudioNTP and AudioMNTP? Are both necessary?**
We address the request in **"1. Presentation Improvement"**. Specifically, we clarify that **AudioMNTP** is our main proposed model. However, introducing **AudioNTP** is also necessary, as there was no existing diffusion-based audio language model baseline in the literature. Therefore, we propose **AudioNTP** as the first such baseline and improve upon it with **AudioMNTP**.
### **Question 2: Why use MLP architecture for the diffusion-based section? Any consideration for other architectures?**
We address the requests in **"1. Presentation Improvement"** and **"8. Inference Time"**. **"1. Presentation Improvement"** clarifies the step-by-step inference pipeline and explains why using a simple MLP is critical for inference (for real-time usage). **"8. Inference Time"** provides inference time results and compares them to several baselines. Our model achieves real-time performance, whereas conventional diffusion models fall short of real-time capabilities. Furthermore, Table 4 in our paper shows that even a modest increase in the diffusion head’s complexity leads to a notable increase in overall latency. Therefore, we do not consider more sophisticated architectures such as Transformers.
### **Question 3: What is the overall structure of the model, is the proposed model mainly replacing the previous LDM/transformer-based feature generation model with the transformer-based decoder?**
We address the request in **"1. Presentation Improvement"**. We provide three new figures to illustrate the overall structure of the model and explain the training and inference pipelines step by step. We also clarify the differences between our proposed approach and simply replacing the previous LDM/Transformer-based feature generation model with a Transformer-based decoder.
### **Question 4: Can we provide some demos of the result?**
We address the request in **"3. Demos"**. Our demo page provides pairwise comparisons between AudioMNTP and several baselines, demonstrating the effectiveness of our method.
### **Question 5: What is the inference time of the proposed model?**
We address the request in **"8. Inference time"**. The inference results suggest that our proposed model achieves real-time performance and is significantly faster than conventional diffusion models. Also, our model is comparably fast to discrete Audio LMs but provides much better generation quality.
### **Question 6: Why the evaluation in Table 2 being categorized into non-speech and speech? Does that mean the model can successfully generate real-speech content?**
We address the request in **"5. Why split into speech vs. non-speech?"**. Specifically, we explain the rationale behind this division and propose renaming the categories to **pure sound** and **sound + speech** to avoid confusion. We also clarify that most TTA systems — including ours — cannot generate intelligible speech.
# Additional requests we infer from the comments
---
### **Additional baselines for diffusion-based Audio LM**
> The authors claim that previous diffusion-based audio language models present bottlenecks and limitations. However, evidence supporting the effectiveness and superiority of the proposed AudioMNTP models over simpler baselines is not adequately provided.
We address the request in **"2. Does not compare to Diffusion-Based Audio LM Baselines"**. Specifically, we point out that there is no prior diffusion-based audio LM for TTA. As a result, we propose the first such model, AudioNTP, as a strong baseline. Our AudioMNTP further improves upon AudioNTP and several existing baselines, including discrete LMs and diffusion models. The effectiveness and superiority of our method are supported by both objective metrics and the newly provided demo page.
---
We thank the reviewer again for the valuable feedback. As shown in the above point-by-point rebuttal, we believe our original response has addressed your requests. If there are any remaining concerns, we would greatly appreciate it if you could point them out in more detail. We are happy to further clarify or make additional improvements! | Summary: This paper presents a novel approach for generative audio language modeling using continuous-valued tokens instead of discrete tokens. The key contributions include:
1. Following previous works, such as masked autoregressive (MAR), which introducing continuous-valued audio tokens to replace discrete ones, improving generative modeling by preserving more information.
2. Proposing a novel Masked Next-Token Prediction (MNTP) learning task that enhances next-token prediction by incorporating masked token prediction.
3. Demonstrating that their approach achieves significant improvements over AudioGen and UniAudio.
4. Achieving results comparable to state-of-the-art diffusion models while maintaining a more efficient and streamable transformer-based causal language modeling framework.
5. Validating the approach with extensive quantitative and qualitative evaluations, including human evaluation on speech and non-speech audio generation.
Claims And Evidence: The claims made in the submission is supported by clear and convincing evidence.
1. The claim that continuous-valued tokens lead to better generation quality is validated by improvements in FAD and KL divergence compared to discrete-token-based models like AudioGen.
2. The effectiveness of MNTP is demonstrated through significant improvements over their baseline AudioNTP model, suggesting that masked token prediction enhances next-token prediction.
Methods And Evaluation Criteria: The proposed methods, including the use of continuous-valued tokens and MNTP, are well-motivated and clearly explained.
The choice of evaluation metrics (FAD, KL divergence, IS, CLAP score, and subjective human ratings) is appropriate and widely used in audio generation tasks.
Theoretical Claims: This paper is experiment-driven research. Without any theoretical claims.
Experimental Designs Or Analyses: The experimental designs effectively validate the proposed method in the appropriate benchmarks and comparisons.
Supplementary Material: I carefully review all of the supplementary parts.
Relation To Broader Scientific Literature: This study follows the continous LM training strategies in image/audio generation. Although the idea is not novel, this paper validates the effectiveness of such training strategy in audio generation domain. Futhermore, they also introduce masked next-token
prediction (MNTP) strategy.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Weaknesses:
1. The paper does not include a detailed comparison of inference latency between their model and diffusion-based methods, which would be critical for real-time applications.
2. The proposed MNTP schedule needs more discussion:
(1) The authors point out that "Recent works show that dropping instead of masking yields similar performances while greatly reduce the training cost". Whether authors conduct experiments to support this claim?
(2) What is the max mask ratio for MNTP?
(3) which types of positional encoding?
Other Comments Or Suggestions: Refer to Weaknesses parts.
Questions For Authors: Can you give more explanation about the design of target positional embedding? From Figure 3, I can only find the it starts from BOS token. I cannot fully understand it's value.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # 1. Inference Latency Comparison with Diffusion Models
We appreciate the reviewer’s comment and will include a latency discussion in the final version. We present the latency comparison in Table A.
**Table A. Latency comparison of TTA models**. Measured with **batch size = 1** on a single NVIDIA A100 using 10-second clips. RTF = inference time / 10 sec. **Bold**: best; *Italic*: second best. AudioGen Base has no reported latency.
| Model | Type | Param | Latency (s) ↓ | RTF ↓ | FD ↓ | FAD ↓ | KL ↓ | IS ↑ | CLAP ↑ |
|--------------------|----------------|--------|----------------|---------|---------|--------|--------|---------|----------|
| AudioLDM 2 | Diffusion | 346M | 32.03 | 3.203 | 32.14 | 2.17 | 1.62 | 6.92 | 0.273 |
| AudioLDM 2 Large | Diffusion | 712M | 65.23 | 6.523 | 33.18 | 2.12 | 1.54 | 8.29 | 0.281 |
| Tango 2 | Diffusion | 866M | 60.77 | 6.077 | 20.66 | 2.69 | **1.12** | 9.09 | **0.375** |
| AudioGen Base | Discrete LM | 285M | - | - | - | 2.84 | 2.14 | - | - |
| AudioGen Large | Discrete LM | 1B | **12.4** | **1.24**| - | 1.82 | 1.69 | - | - |
| **AudioMNTP Base** | Continuous LM | 193M | *13.43* | *1.343* | *14.81* | *1.68* | *1.16* | *9.67* | 0.336 |
| **AudioMNTP Large**| Continuous LM | 462M | 15.77 | 1.577 | **14.3**| **1.22** | 1.17 | **9.81**| *0.341* |
#### **AudioMNTP v.s. Diffusion Models**
AudioMNTP Base and Large achieve much lower latency and better quality than diffusion models. This is due to using a small MLP for diffusion steps, instead of repeatedly applying the full model. Over 90% of the parameters run only once per token.
> The token sequence is 256 long—much shorter than the typical 1000+ denoising steps used in diffusion models.
#### **AudioMNTP v.s. AudioGen**
Compared to AudioGen Large, AudioMNTP gives much better quality with only a small latency increase. Both use a single-pass Transformer, but AudioMNTP replaces the single-pass categorical head with a multi-pass diffusion MLP. The added diffusion steps greatly boost generation quality with a slightly higher latency.
#### **Real-Time Applications**
Only AudioGen and AudioMNTP reach near real-time generation (RTF ≈ 1). On an H100 GPU, real-time is easily achievable. Diffusion models remain too slow for such use cases.
# 2. Discussion on MNTP Schedule
#### **Masking v.s. Dropping**
Table 3 (rows C–E) shows similar results for zero masking, Gaussian masking, and dropping:
| Masking Scheme | FD ↓ | FAD ↓ | KL ↓ | IS ↑ | CLAP ↑ |
|--------------------|-------|-------|-------|-------|--------|
| Zero Masking | 16.78 | 1.97 | 1.28 | 9.33 | 0.333 |
| Gaussian Masking | 15.15 | 1.82 | 1.18 | 9.22 | 0.324 |
| Dropping | 16.62 | 1.77 | 1.32 | 9.25 | 0.315 |
We chose dropping due to its lower compute cost, which improves efficiency and scalability.
#### **Max Mask Ratio**
We sample mask ratios from \[0, 1\]. When the ratio hits 1, we retain one random token and use the BOS token and positional embedding to predict it. We’ll clarify this—thank you for the observation.
#### **Positional Encoding**
We use **absolute positional embeddings**, as both training and inference operate on 10s clips. Extending this to longer sequences using RoPE is a promising direction for future work.
#### **Can you give more explanation about the design of target positional embedding?**
Certainly! Traditional prediction always targets the immediate next token. **MNTP**, in contrast, predicts tokens at variable distances. For instance, if the sequence is **0, 3, 6, 9**, token 3 predicts 6, not 4. Since the offset varies, the model can't guess the target from context alone.
To help, we add a **target positional embedding** that tells the model which position to predict.
In **Figure 3**, each token predicts the next unmasked token at a variable offset. The embedding $p_t$ encodes this offset (e.g., $x^0 + p_t^3$ → $x^3$, $x^3 + p_t^5$ → $x^5$). We use absolute embeddings for $p_t$.
Thanks again—we agree the paper’s explanation was brief and will expand it in the revision.
# 3. Demo
We didn’t include the demo in the original submission. It’s now live at [https://audiomntp.github.io/](https://audiomntp.github.io/). Please have a look!
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We truly appreciate your feedback. It helped improve the paper in concrete ways. If you feel your concerns are resolved, we’d be grateful if you could consider a higher score. Let us know if there's anything else we can improve. Thank you again!
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Rebuttal Comment 1.1:
Comment: Thank you for your thorough and constructive response. My concerns have now been fully addressed. I maintain my initial overall assessment leaning towards acceptance.
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Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for the kind words! If all concerns are addressed, would you consider a higher score? | Summary: This paper investigates generative audio language modeling with continuous-valued tokens. It begins with a next-token prediction approach in which each latent embedding (i.e., token) from an autoencoder is iteratively produced via a token-wise diffusion process. Building on this, the authors propose Masked Next-Token Prediction (MNTP), a strategy that predicts future tokens rather than strictly the next one. Experimental results demonstrate that MNTP not only improves both next-token and masked-token prediction but also matches or surpasses strong audio generation baselines. Furthermore, an extensive ablation study covering architecture design, training objectives, and token masking techniques, highlights the impact of each component on the model’s overall effectiveness.
## update after rebuttal
I appreciate the authors' response to my concerns. Although the rebuttal did not present extensive new experimental evidence on those concerns, the work’s potential impact on its field remains noteworthy, albeit not groundbreaking. Consequently, I maintain my initial overall assessment leaning towards acceptance.
Claims And Evidence: The proposed methods and evaluation criteria are relevant.
Methods And Evaluation Criteria: Proposed methods and/or evaluation criteria are reasonable and aligned with the problem/application.
Theoretical Claims: I reviewed proposed methods and found them sound.
Experimental Designs Or Analyses: I reviewed the experimental design and analyses and found them sound.
Supplementary Material: I reviewed Ablating the components of MNTP and Masking Schedules.
Relation To Broader Scientific Literature: This work contributes to improving language modeling in the audio domain and introduces innovations to further enhance generative performance, which could also be applicable or relevant to other generative modeling domains, such as image generation or text-to-speech.
Essential References Not Discussed: Essential references are well discussed.
Other Strengths And Weaknesses: Strengths:
* The proposed Masked Next-Token Prediction (MNTP) approach is both conceptually simple and effective. It delivers stronger results than standard next-token or masked-token prediction techniques.
* The authors' explanations throughout the manuscript, including insightful footnotes, effectively highlight the contributions of this work and clearly distinguish it from other methods. Their detailed discussion enriches the understanding of both the proposed method and experimental analysis.
* The authors conducted extensive and rigorous experiments, providing comprehensive results. The detailed ablation study, covering architecture variations, training objectives, and token masking strategies, clearly illustrates how each individual component contributes to the overall performance and effectiveness of the method.
Weaknesses:
* Only two model size variants (base and large) are considered, with an ablation study limited to the size of the MLP-based diffusion module. Including additional experiments focused on scalability, both in terms of model size and dataset size, would offer deeper insights into the proposed approach’s potential at larger scales.
* The method is currently evaluated exclusively on language modeling involving continuous-valued tokens, leaving uncertainty regarding its applicability to discrete-valued tokens. Exploring the effectiveness of MNTP when applied to token sequences generated by vector-quantized VAEs, for example, could broaden its scope and demonstrate greater versatility.
Other Comments Or Suggestions: Page 6, line 326: Typo – “(2) our model is significantly smaller, i.e., 866M Tango 2.”
Questions For Authors: I don't have any other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are sincerely grateful for your kind words and thoughful comments. Regarding our weaknesses, we address them in the following:
# 1. Larger scale in both model size and dataset
We fully agree that exploring the scaling behavior of our proposed methods would provide valuable insights. In this current submission, our primary focus is on introducing continuous-valued tokens and the MNTP method. With smaller-scale models and datasets, we achieve SOTA performance, justifying the effectiveness of our proposal. Nonetheless, we acknowledge the importance of examining whether these methods maintain their effectiveness at larger scales.
We have preliminary evidence of scaling effectiveness, where increasing model parameters from Base to Large by approximately 140% led to notable improvements in overall performance metrics. This positive trend is noteworthy, especially given that such improvements are not universally observed, as exemplified by the comparative performance of AudioLDM-full vs. AudioLDM-full Large and Magnet small vs. Magnet large.
We agree that scaling analyses are broadly relevant in the context of large language models. We would be eager to further investigate scalability; however, the substantial increase in convergence time and resource requirements associated with training larger models and datasets means we cannot provide these results during the rebuttal period. Should our submission be accepted, we commit to including detailed scalability analyses in the final manuscript.
> **Note.** As a practical consideration, training the Large model on AudioSet, similar to the approach adopted by AudioGen, requires approximately one month of computational resources utilizing around 100 V100 GPUs. Even scaling down to the Base model demands around two weeks of training. These estimates do not account for the additional resources necessary to explore even larger model configurations.
# 2. Generalizability of MNTP to discrete tokens
Thanks again for the helpful comments! In this work, our primary claim emphasizes that both continuous-valued tokens and MNTP are crucial for achieving SOTA audio generation using language models, supporting MNTP's efficacy specifically for continuous data. However, extending MNTP methodologies to discrete tokens is indeed a compelling new direction and will be part of our future research efforts. We appreciate your suggestion!
# 3. Typo
We will fix the typo. Thanks for the comment!
# 4. Demo
We omitted the demo from our initial submission. Here is our [demo page](https://audiomntp.github.io/). Please take a look!
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We appreciate your valuable comments! If you feel we have adequately addressed your concerns, please consider increasing the score. If you have any further suggestions for improving our paper, please do not hesitate to let us know. Thank you!
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Rebuttal Comment 1.1:
Comment: I appreciate the authors' response to my concerns. Although the rebuttal did not present extensive new experimental evidence on those concerns, the work’s potential impact on its field remains noteworthy, albeit not groundbreaking. Consequently, I maintain my initial overall assessment leaning towards acceptance.
To further highlight and broaden contributions of this work, it would be beneficial to include additional experimental results. Specifically, providing evidence regarding the scalability of this approach could effectively highlight its advantages over competitive methods, aligning with the points raised by Reviewer eX1D regarding works like Audiobox. This aspect is particularly relevant given the rapid advancements in text-to-audio generation, exemplified by recent work like TangoFlux (I mention this purely for context regarding the field's progress, not necessarily requiring discussion or citation). Additionally, showing the MNTP module's potential applicability to discrete tokenization, which is widely used in other domains such as text-to-speech or image generation, could significantly broaden the perceived impact of this work.
Please let me know if I have misunderstood the authors’ response, if my comments extend beyond the initial concerns, or if the authors believe that they have already adequately addressed most of the reviewers’ requests.
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Reply to Comment 1.1.1:
Comment: We thanks the reviewer for the kind word! We believe we are aligned with the reviewer points:
1. The large-scale results would further highlight the advantage of our approach, given the evidences shown by LLM
2. The applicability of MNTP to discrete tokens would further broaden the impact of our proposal, given that discrete LM is the mainstream.
We fully agree with the above comments, and we summarize our responses into key messages:
1. We wish to highlight that our method using small-scale model and data successfully outperforms several established baselines, all of which use large-scale models and data—serving as strong evidence of our method's effectiveness. Our scalability results, from the small (190M) model to the medium (460M) model, also verifies scalability within a range we can afford. What we lack is the large-scale result (i.e. 1B), which are highly resource demanding. The reviewer highlights the benefit of this further study and still accepts our paper. We plan to incorporate the large-scale results but cannot provide numbers at this point due to time constraints.
2. Our scope in this paper is primarily focused on introducing the first continuous-valued audio language model (LM) for TTA, and on further improving it. Therefore, studying MNTP's effectiveness on discrete tokens may be somewhat out of scope, as MNTP remains critical for continuous LMs regardless of its effectiveness on discrete LMs. However, we fully agree with the reviewer's point that such a study could significantly broaden MNTP's applicability. As such, we believe it would be more appropriate to explore this topic in a separate paper specifically focused on the discrete use case.
We thank the reviewer for all the responses. We believe there is no misunderstanding. Thank you! | null | null | null | null | null | null | null | null |
ResKoopNet: Learning Koopman Representations for Complex Dynamics with Spectral Residuals | Accept (poster) | Summary: This paper introduces a new deep learning based approach for approximating Koopman eigenvalues based on Residual DMD. By learning a dictionary representation that minimizes a spectral residual loss function, the authors demonstrate their approach is able to perform well on several data sets.
Claims And Evidence: All major claims are supported by clear evidence.
Methods And Evaluation Criteria: The authors evaluate their computational framework on two benchmark data sets (pendulum and turbulence) and one data set that has not been frequently studied (mouse neural activity). The authors compare their approach to several different methods that are commonly used, and appear to make the comparisons fairly.
Theoretical Claims: I did not follow the discussion of Barron spaces and convergence in Appendix A.3. This is not my expertise, but I did feel that the introduction to Barron spaces was a little terse and it was not clear to me why one would expect them to be appropriate spaces to consider for ResKoopNet, since the networks used were three layers (Sec. 3.2 -- not two layers, as mentioned in Appendix A.3).
Experimental Designs Or Analyses: The experiments were largely well done, but I have several specific comments/questions:
1. The authors claim that ResDMD requires 964 dictionary elements to compute the pseudospectra of the nonlinear pendulum (Sec. 4.1). However, Fig. 1 of Colbrook and Townsend (2024) only shows the spectra computed for 150 and 964 dictionary elements. The authors show that 300 dictionary elements does not lead to the complete pseudospectra (Fig. 4), but they do not show that at least 964 are needed. It could be that significantly fewer dictionary elements than 964 are needed (but greater than 300). I think therefore this claim should be modified.
2. The authors show that the higher Koopman modes computed by ResKoopNet approximate acoustics in the turbulence example. Figs. 5c and d look identical to me. Could this be an error and the same figure plotted twice? If not, is there a reason the 6th and 7th Koopman modes are so similar?
3. The results on using Koopman mode decomposition for clustering neural activity across stimuli is interesting. I think there are three basic analyses that could strengthen these results. First, could the authors plot the neural population recordings (averaged across trials) for each stimuli. Is there a clear difference in the activity across stimuli (in which case, maybe such a dynamics based clustering is not necessary). Second, what happens if you cluster the trials just based on the mean activity (for each neuron) across the trial? I could imagine different visual stimuli driving different average activity in the neural population, that could be picked up by the Koopman eigenfunctions associated with eigenvalue 1. And third, what happens if you use fewer Koopman modes, computed from ResKoopNet, in your clustering? It seems like comparing having 500 modes vs. having 50 (in the case of Hankel-DMD) could affect the comparison.
Supplementary Material: I skimmed through all sections of the supplement.
Relation To Broader Scientific Literature: This work could be improved by motivating more clearly why ResDMD is such a powerful method and why using the spectral residual loss function is so important. Why not use, for instance, the dictionary learning EDMD to find a good spectral approximation. I think the authors have reasons for this sprinkled throughout the paper, but making it more clear would be helpful. Additionally, the authors discuss dictionary learning EDMD and work showing convergence bounds of EDMD (Korda and Mezic, 2018), but then they also say things like "ResKoopNet employs neural networks to optimize dictionary functions" (page 1) and "EDMD lacks theoretical gaurantees of convergence" (page 1), without discussing this highly relevant work. Finally, the authors say that "as shown in (6), ResKoopNet provides an explicit expression for $\tilde{K}$" (page 3). But this expression is just from EDMD, and not specific to ResKoopNet. These last two points give slightly misleading representations on what this works contributions are.
Essential References Not Discussed: The authors cited everything that I think is essential (but could use with more referencing of those works throughout the text, as noted above).
Other Strengths And Weaknesses: **Strengths**
1. I thought the idea of using the residual spectral loss was innovate and appeared to lead to strong results.
2. The application of ResKoopNet to neural data (while I have some reservations about it, see above) is novel and interesting.
3. Developing better tools for approximating the continuous part of the Koopman spectra is important and I think a contribution of this paper (that could even be discussed more in the intro).
**Weaknesses**
1. The experimental results could be improved, as discussed above.
2. The authors could make their contributions more clear (and not make claims that could be misleading about their contributions), as discussed above.
3. The authors could make the paper easier to follow by including more discussion on ResDMD, particularly on Kernel ResDMD, since they compare to this method several times. Additionally, writing out the Koopman mode decomposition could allow the authors to introduce Koopman methods better. Finally, explaining why the true pseudospectra covers the entire unit circle in Sec. 4.1 would be helpful.
4. Finally, there are a number of typos and grammatical errors throughout the paper. While I very much understand the presence of these things, the amount was bordering on making it harder to read.
Other Comments Or Suggestions: The authors rely a number of times on referencing results from the original ResDMD paper. This makes it harder for the reader who is not very familiar with ResDMD to follow at places, and to compare the results. I think one last way for the authors to improve their paper is to include more results/discussion to make the paper as self contained as possible, even if this all this additional information is added to the Appendices.
Questions For Authors: 1. Are Fig. 5c and d the same figure? If not, why are the modes so similar?
2. How much do the clustering results in Fig. 6 rely on the learned dynamics (as opposed to the trial average responses of the neurons/mean firing rate for each stimuli)? How dependent are they on the exact number of Koopman eigenfunctions used for ResKoopNet?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: 1. Thank you for your insightful suggestions. The updated figures and proof can be seen here: https://anonymous.4open.science/r/rebuttal_materials-14918/
2. Thank you for raising this point about Barron spaces and the network architecture. To clarify, Barron spaces (Appendix A.3) provide a theoretical framework for analyzing functions efficiently approximated by neural networks with certain properties. Their mathematical properties, notably being dense in $L^2$ spaces under certain conditions, ensure that functions in $L^2$ can be approximated arbitrarily well by Barron functions. This justifies applying Theorem A.3 and supports our extended analysis (see the file **convergence_proof.pdf**).
3. Regarding the network architecture notation: the “2-layer” network mentioned in the theorem refers to a single hidden layer plus an output layer, which is the standard notion in approximation theory. Practically, we used three hidden layers (Section 3.2) for improved empirical performance, but insights from the 2-layer theory still inform deeper network convergence behavior (see **convergence_proof.pdf**).
4. The convergence analysis in Section A.4 relies on this framework because it establishes that as the number of neurons increases, the approximation error decreases at a specific rate (proportional to $1/\sqrt{r}$ where $r$ is the number of neurons). This gives us confidence that with sufficiently large networks, ResKoopNet can theoretically approximate the true Koopman eigenfunctions with quantifiable error bounds, which is essential for the spectral analysis guarantees we discuss (see **convergence_proof.pdf**).
5. You are correct that the original ResDMD requires fewer basis functions. We discuss this further and include a new experiment (**Fig_7.png**). Still, results show that ResDMD needs around 500 manually selected dictionary elements, whereas ResKoopNet achieves better performance with only 300 basis functions without manual selection.
6. Regarding Fig. 5(c) and (d): You are correct; these were identical due to complex conjugate eigenvalues. In the updated version (**Fig_5_new.png**), we've repeated the experiment using 250 dictionary elements (matching ResDMD from Colbrook & Townsend, 2024), resulting in distinct Figures 5(c) and (d). We have also added singular value plots in the new Figures 5(e) and (f).
7. Regarding the neural experiment, as suggested by the reviewer, we have included new figures:
(1) To ensure a fair comparison with the 50 bases in Hankel-DMD, we re-estimated the Koopman eigenfunction from ResKoopNet using 50 dictionaries (24 SVD truncated bases, one constant, and 25 trainable bases). As a result, the performance is similarly good to the performance with 501 bases. For details of approximated averaged eigenfunctions and clustering results please refer to **Fig_6_new.png, Fig_13.png and Fig_16.png**. A hyperparameter scanning is also included in **Fig_17.png**.
(2) The reviewer is right to point out that both the averaged response across trials and the mean firing rates are sufficiently distinct for each video stimulus. **Fig_10.png** shows trial-averaged neural activities for an example mouse, and **Fig_11.png(A)** presents mean firing rates across all mice for the six stimuli.**Fig_11.png(B–D)** demonstrates clustering directly based on mean firing rates, confirming that mean firing rate information alone is sufficient, with performance comparable to ResKoopNet (**Fig_12.png**).
(3) We agree clustering via Koopman eigenfunctions is biologically not strictly necessary here given the clear stimulus-driven differences. However, this dataset provides an ideal benchmark for Koopman eigenfunction estimation methods. Notably, standard approaches like Hankel DMD, kernel ResDMD, and EDMD (RBF basis) fail to differentiate these distinct processes, likely due to limitations in handling high-dimensional data or eigenfunction estimation.
(4)The effectiveness of ResKoopNet in accurately estimating Koopman eigenfunctions demonstrates its strength and broader applicability, particularly for more challenging tasks such as unsupervised latent brain state identification or decoding/reconstructing object movements from the videos, forming promising directions for future research.
8. Regarding 'Why not use, for instance, the dictionary learning EDMD to find a good spectral approximation': The Koopman matrix updating formula $\tilde{K}$ (Eq.6) matches EDMD, but it is derived from a distinct loss function (Eq.5), as shown in Appendix A.2. This loss function difference is fundamental; ResDMD (via Galerkin approximation, Eq.(2)) approximates both $\mathcal{K}$ and $\mathcal{K}^*\mathcal{K}$, whereas EDMD approximates only $\mathcal{K}$. Thus, during optimization, ResKoopNet yields a $\tilde{K}$ that better captures Koopman's spectral properties.
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Rebuttal Comment 1.1:
Comment: I appreciate the authors thorough response to my questions. The answers have sufficiently addressed my questions/concerns. I am going to maintain my score of a 3, however I feel more confident in that score and more confident in supporting this paper.
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Reply to Comment 1.1.1:
Comment: Thank you for your comments and for taking the time to review our paper. I'm glad to hear that our responses helped clarify your concern and increased your confidence in the work. | Summary: This research presents a novel method for approximating the spectral components of the Koopman operator for discrete-time deterministic dynamical systems by minimizing spectral residuals. Unlike traditional methods that rely on predefined dictionaries, this approach utilizes a neural network to optimize dictionary functions to discover a more precise and complete spectrum of the Koopman operator for complex dynamical systems. The method employs an alternating optimization procedure, where a neural network learns the suitable observables while the Koopman matrix is iteratively updated via least-squares estimation. The method's effectiveness is validated on a pendulum system, a turbulence model, and neural recordings, demonstrating superior accuracy over classical methods.1
Claims And Evidence: 1. The authors claim that their method addresses spectral inclusion and reduces spectral pollution for complex dynamical systems of high dimensions, which is not well-supported. In none of the experiments do they show that there exists a subset of the true spectrum that is not attainable from ResDMD or other methods, but instead that their method can do that. In Experiment 1, which is a low-dimensional system, they only show that for finding the whole spectrum, ResDMD needs a bigger size dictionary. Also, it is noteworthy that Hankel-DMD works almost as well as the proposed method. In Experiment 2, the authors do not directly compare their method with ResDMD using the same size dictionary. While they are using Nk = 300, the figures in the ResDMD are when Nk = 250. This problem also exists in the last experiments, and the size of the dictionaries is very different. So in a nutshell, for the first experiment (low-dim) they did not show that they are able to find some part of the spectrum that the other methods cannot, and for the others (high-dim) the comparison is not fair in my opinion. Thus, I would suggest the authors provide more evidence to support their argument.
2. The authors use the term “optimal” representation several times in the paper, but they do not specify in which sense the neural network's learned representation is optimal. How do they know that? Since the cost function they are using is an estimate of spectral residual, with a finite number of samples, one cannot be sure that if it is small, it means that the real object is also small. Furthermore, there might be noise in the data.
3. In addition, the claim for convergence analysis is a bit shaky, which I will elaborate on in the theoretical claims section.
Methods And Evaluation Criteria: Yes, the proposed method is sensible in general. Using neural networks to learn representations for the Koopman operator is a well-known technique in the field. Also, the datasets used are aligned with the proposed method and the problem. However, I am not sure that the evaluation criteria for showing the superiority of the methods make sense if there is not a fair comparison between different methods.
Theoretical Claims: Yes, I checked all the theoretical claims in the appendix. The authors demonstrate equivalences between different equations presented in the main body of the paper, which appear correct. However, the convergence analysis is, in my opinion, somewhat shaky. First, the proposed method uses a three-layer neural network, whereas the theory provided is for two-layer networks. Second, the norm of the functions derived from density arguments is unknown. Thus, as we considering sum of the norm of these functions for each mode it is not clear how one might ensure the epsilon guarantee.
Experimental Designs Or Analyses: I checked the experiments and analysis. As I mentioned before, the experiment design could be improved to make the comparison more fair.
Supplementary Material: Yes, I checked all the supplementary materials, though not in detail.
Relation To Broader Scientific Literature: The key contributions of the paper build upon prior advancements in Koopman operator theory, particularly addressing limitations in existing spectral approximation methods such as Extended Dynamic Mode Decomposition (EDMD) (Williams et al., 2015) and Residual Dynamic Mode Decomposition (ResDMD) (Colbrook & Townsend, 2024). While EDMD provides a finite-dimensional approximation of the Koopman operator, it suffers from spectral pollution and lacks guarantees of capturing the full spectrum, especially in high-dimensional systems. ResDMD improves upon this by introducing spectral residuals to filter inaccurate eigenvalues, but it still relies on predefined dictionaries and does not refine spectral estimates. ResKoopNet advances this line of research by optimizing dictionary functions through a neural network, thus addressing the spectral inclusion problem and improving spectral accuracy. This aligns with recent trends in machine learning-assisted dynamical systems analysis, such as deep autoencoders for Koopman embeddings (Lusch et al., 2018) and kernel-based Koopman methods (Kevrekidis et al., 2016), but differs in its explicit spectral residual minimization approach.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper is highly original in its integration of spectral residual minimization with neural network-based dictionary learning, addressing key limitations of existing Koopman approximation methods. Its significance lies in improving spectral accuracy for complex dynamical systems, with strong implications for physics, engineering, and neuroscience. In terms of clarity, the paper is generally well-written and the concepts are explained in a logical flow. Overall, the paper presents an important contribution but would benefit from broader benchmarking and a clearer discussion of trade-offs.
Other Comments Or Suggestions: Typos:
“ … its only filters precomputed spectra …” → “... it only filters …”
"... These results are presented in Appendix Figure 7 and Appenxic A.7.2." → appendix A.7.2
“In this chapter ..” → “In this section…”
Questions For Authors: 1. The authors only compared their method with classical methods, which use kernel functions. I wonder if there are any DMD methods leveraging neural networks that could be included for comparison?
2. It is unclear how the authors determined the hyperparameters for the proposed method and the other methods. I wonder if hyperparameter tuning was performed, especially since some of the comparison methods are kernel methods, where using different kernel functions might yield different results. If yes, I think it will be great to mention to it in the main body.
3. In the turbulence experiment, the color maps vary across different Koopman modes and methods. Would it be possible to use normalized Koopman modes to better facilitate comparison and verification of the results?
4. The authors reported that despite having small residuals, the Hankel-DMD modes fail to clearly capture the fundamental pressure field structure. Does this not suggest that the residual metric may not be a reliable indicator of representational quality, and thus the final representation may not be truly “optimal”?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: 1. We would like to thank the reviewer for the helpful comments. The updated figures and proof can be seen here: https://anonymous.4open.science/r/rebuttal_materials-14918/
2. Regarding “Hankel-DMD works almost as well as the proposed method”: While Hankel-DMD performs well in Experiment 1's lower-dimensional case, it underperforms in Experiments 2 and 3's higher-dimensional settings. We included it across all experiments for consistency and fair comparison. In Experiment 2, ResKoopNet successfully captured a dominant Koopman mode showing the main air pressure structure near the airfoil that both ResDMD and Hankel-DMD missed (see ResDMD Fig.17 and our Appendix Fig.7) In Experiment 3, ResKoopNet succeeded whereas Hankel-DMD and others failed. These results show that our method addresses the spectral inclusion by capturing important spectral components that other methods miss.
3. We acknowledge that our original turbulence example used 300 basis functions, while ResDMD used 250. We re-did the experiment and the updated results are shown in **Fig_5_new.png**.
4. In the neural experiment, to ensure a fair comparison with the 50 bases in Hankel-DMD, we re-estimated Koopman eigenfunctions from ResKoopNet using 50 dictionary elements (24 SVD-truncated bases, one constant, and 25 trainable bases). The resulting performance is comparably strong to the original 501-basis case. Detailed approximations of eigenfunctions and clustering outcomes are provided in the updated **Fig_6_new.png, Fig_13.png and Fig_16.png**.
5. Regarding the optimality comments:
(1) Regarding the comment that ‘in which sense the neural network's learned representation is optimal’: the ‘optimal’ representation in ResKoopNet is not optimal in the classical sense (e.g. a unique minimizer of an L2 error as in EDMD); rather, it means that the learned dictionary minimizes a very specific loss: ‘spectral residual’ so that the finite-dimensional Koopman operator best captures the true spectral properties (both discrete and continuous as explained in ResDMD of the underlying Koopman operator given the data. In other words, by minimizing the spectral residual, the network is trained to produce a dictionary (or representation) that ‘optimally’ balances the ability to approximate the Koopman eigenpairs against the error introduced by discretization and finite sampling. Minimizing this loss(Eq.7 in the paper) pushes the network toward a representation where the computed eigenpairs have a very low spectral residual.
(2) Regarding the comment that 'with a finite number of samples, one cannot be sure that if it is small, it means that the real object is also small', the authors justify the 'optimality' by proving convergence results in Appendix A.4(see **convergence_proof.pdf**): as the number of samples increases and as spectral residual loss function $J(\theta)$ below a threshold, the approximation of the dictionary converges (and hence the `optimality’ hold). So while practically the cost function is an estimate, the theory from ResDMD assures that, in the limit, a near-zero cost implies a good approximation of the true Koopman spectrum.
(3) Additionally, the convergence analysis in Appendix A.4 (pages 14–15, in red) is expanded to demonstrate the convergence of both the dictionary and the spectrum, see **convergence_proof.pdf**.
(4) The data may contain noise, but our work uses a deterministic framework without accounting for stochastic effects. We plan to address noise and stochasticity in future research (see the Conclusion Section (second paragraph)).
6. Regarding other DMD methods with neural networks: Since ResDMD is EDMD-based, we compared it with EDMD-DL(Li et al., 2017). ResDMD and kernel-ResDMD have full spectrum theoretical guarantees but do not address spectral inclusion issues, while EDMD and EDMD-DL are effective in both low and high dimensions, they lack similar guarantees as ResDMD. Future work will explore advanced neural network structures, e.g., PINO or KAN, and include further comparison with other neural network-based DMD methods.
7. We performed hyperparameter tuning and included them in **Fig_8.png**, demonstrating the robustness of our parameter choices. The hyperparameter scanning results for the neural experiment are included in **Fig_17.png**: with smaller layer size and layer number, the clustering performance is not stable but becomes robust after the two hyperparameters reach a threshold. Therefore we have chosen 3 layers of 200 neurons.
8. We have now used the same normalized color map value for each Koopman mode figure (**Fig_5_new.png**).
Hankel-DMD does not perform as well as ResKoopNet in Fig. 7 of Appendix A7.2 because its foundation(Takens’ embedding) is different from the Galerkin framework used in EDMD and ResDMD, from which the spectral residual metric is derived. Thus, even a small residual for Hankel-DMD may not capture key dynamics (like the main pressure field structure and clustering brain state). | Summary: The paper focuses on Koopman operator analysis and builds on the Residual Dynamic Mode Decomposition (ResDMD), which uses the spectral residual to evaluat the accuracy of a Koopman operator approximation and to perform filtering of a computed spectrum. Here, the proposal is to use the spectral residual iteratively during the spectral estimation process, iterating between optimizing a neural network that parameterizes a dictionary and minimizing the residual to identify the Koopman eigenpairs. The paper reports numerical experiments for multiple systems/datasets including a pendulum system, a turbulence system, and neural recordings from the visual cortex of mice.
Claims And Evidence: Please see "Other Strengths and Weaknesses"
Methods And Evaluation Criteria: Please see "Other Strengths and Weaknesses"
Theoretical Claims: I checked the provided calculation steps in Appendices A.1 and A.2.
Experimental Designs Or Analyses: Please see "Other Strengths and Weaknesses"
Supplementary Material: I carefully read all of the appendices. I briefly inspected the code.
Relation To Broader Scientific Literature: Please see "Other Strengths and Weaknesses"
Essential References Not Discussed: [R1] Colbrook, Matthew J. "Another look at Residual Dynamic Mode Decomposition in the regime of fewer Snapshots than Dictionary Size." Physica D: Nonlinear Phenomena 469 (2024): 134341.
Other Strengths And Weaknesses: Strengths
S1. The paper introduces a novel Koopman analysis framework.
S2. The reported experiments are thorough and the results demonstrate a noticeable improvement over existing techniques.
S3. Section 4.3 is particularly interesting and highlights the strengths of the proposed methods in terms of its ability to capture key dynamics and perform effective clustering.
S4. The paper provides a good discussion of relationships to other neural-network based Koopman operator frameworks (Appendix A.4).
S5. The discussion of the computational costs (Appendix A.5) is helpful.
S6. There is good detail and justification for experimental design choices (Appendix A.9)
S7. The visualizations and clustering quality analysis, and related discussion, provide valuable insight into the behaviour of the proposed method (Appendix A.9).
Weaknesses
W1. The paper’s novel technical contribution is limited. The paper does not cite [R1] (available from 30. Aug 2024), which outlines an algorithm (Algorithms 7 and 8) to compute the pseudospectra by minimizing the residual. This appears to be identical to the minimization proposed here for a fixed dictionary. Given that this component of the algorithm has already been published, the remaining innovation of this paper consists of incorporating a neural network to parameterize the basis functions and iterating between the minimization steps. As the authors acknowledge, this approach has been widely used in the neural Koopman operator literature, albeit with the focus on the prediction-based loss function (e.g., Li et al., 2017).
W2. Despite its key innovation being the introduction of a neural network to jointly learn the dictionary while minimizing the spectral residuals to determine the Koopman eigenpairs, the experimental section of the paper does not explore any design choices related to the neural network (architecture, layers, convergence, etc.)
[R1] Colbrook, Matthew J. "Another look at Residual Dynamic Mode Decomposition in the regime of fewer Snapshots than Dictionary Size." Physica D: Nonlinear Phenomena 469 (2024): 134341.
AFTER REBUTTAL:
(1) The authors have clarified the differences between their work and [R1].
(2) There has been further experimental exploration of the architectural choices.
(3) The authors have provided further theoretical results concerning convergence. While these are welcome and strengthen the paper, I would observe that the inclusion of a proof in the rebuttal appears to violate the review process policies, which impose a strict character limit and require that links only contain figures and tables. This inclusion potentially provides the authors of this paper with an unfair advantage. I would like the Area Chair to comment on this.
With the above factors in mind, I have increased my overall score from 2 (weak reject) to 3 (weak accept).
Other Comments Or Suggestions: The paper’s contribution would be considerably stronger if it:
(a) Expanded on the convergence analysis in Appendix A.3. The current analysis is very brief and does not provide a clearly-stated convergence result. The final discussion essentially focuses on the existence of the dictionary rather than the ability of the algorithm to converge to it.
(b) Conducted a more thorough investigation of the potential ways to incorporate the neural network (architectural choices, learning behaviour, convergence). Since this is the major novel contribution of the work, seems neglected in the experimental analysis. I suspect that the authors were unaware of [R1] (or even conducted some of the research associated with this work prior to the emergence of that paper). If this paper were the first to propose minimizing the spectral residual (as well as incorporating a neural network) then the contribution would be more substantial and it would be more reasonable to focus entirely on other non-neural experimental aspects.
{R1] Colbrook, Matthew J. "Another look at Residual Dynamic Mode Decomposition in the regime of fewer Snapshots than Dictionary Size." Physica D: Nonlinear Phenomena 469 (2024): 134341.
Questions For Authors: Q1. It is possible that there is a more meaningful distinction between Algorithms 7 & 8 in [R1] and the procedure proposed here, and that I have misinterpreted one of the algorithms due to notational differences. If so, I would appreciate if the authors could clarify what they perceive as the critical difference.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: 1. We would like to thank the reviewer for the helpful comments and suggestions. The updated figures and proof can be seen here: https://anonymous.4open.science/r/rebuttal_materials-14918/
2. Indeed, we didn’t notice the paper [R1]: "Another Look at Residual Dynamic Mode Decomposition in the Regime of Fewer Snapshots than Dictionary Size" and we would like to thank the reviewer for pointing it out. As the reviewer mentions, we indeed conducted our work before the emergence of [R1]. However, after reading this paper, we confirm that Algorithms 7 and 8 in [R1] are different from our proposed method. We first briefly go over both algorithms here: Algorithm 7 is almost the same as the kernel-ResDMD algorithm in the original ResDMD paper(Colbrook & Townsend (2024)) except for the condition of fewer snapshots than dictionary size. It still computes the $\epsilon$-pseudospectrum and corresponding approximate eigenfunctions as in ResDMD. The grid points $z_j$ serve as a candidate of eigenvalue to be tested on in the 3rd step of Algorithm 7, and will be kept only if its ‘’residual” is smaller than a threshold. However, the dictionary used in ‘’residual” is important. In our ResKoopNet method, the dictionary is obtained by minimizing ‘’spectral residual”, which is theoretically guaranteed by Appendix B.2 in the original ResDMD paper(Colbrook & Townsend (2024)). As for Algorithm 8, it is just a variant of Algorithm 7 where a specific candidate of eigenvalue $\lambda$ replaces the grid points $z_j$. So, we would like to point out that our contribution has nothing to do with any modification of improvement on any specific part in ResDMD such as pseudospectrum, rather we proposed a computing method that exploits the theoretical framework of spectral residual and addresses the **spectral inclusion** problem, and validate it in a few examples including a real-world problem.
3. Based on the reviewer’s suggestion, we have improved the convergence analysis, which is mentioned in the file **convergence_proof.pdf**. Since the function space $\mathcal{F}$ we considered here is $L^2$, we will be able to apply Theorem A.3. Under a few assumptions as in Assumption A.4, we have shown the convergence of the trained dictionary to the optimal dictionary and the convergence of estimated eigenpairs to the true spectrum of the Koopman operator $\mathcal{K}$. Now it not only shows the existence of the dictionary but also shows the convergence of the dictionary and we would like to thank the reviewer for the suggestion.
4. The last part of Section 3.2 named ‘’Computing Algorithm” on page 4 briefly introduces the architectures and layers, etc. We have investigated other parameter settings and tried different layer numbers. Specifically, in the pendulum example, we have scanned the layer number in the range [1,2,3,4] and layer size in the range of [250, 275, 300, 325, 350] and demonstrated the robustness of our parameter choices. This result is shown in **Fig_8.png**. The hyperparameter scanning results for the neural experiment are included in **Fig_17.png**: with smaller layer sizes and layer numbers, the clustering performance is not stable but becomes robust after the two hyperparameters reach a threshold. However, integrating the spectral residual-based Koopman operator approximation method with more complicated neural networks like PINO or KAN is beyond the scope of current work and will be addressed in future extensions. | Summary: The paper introduces ResKoopNet, a neural network-based method for learning Koopman operator representations of high-dimensional nonlinear dynamical systems.
ResKoopNet aims to address limitations of previous methods of learning Koopman operators from data such as Extended Dynamic Mode Decomposition that discover spurious eigenpairs from data, and the spectral inclusion problem related to the difficulty in capturing the entire true spectrum of the Koopman operator, especially for systems with continuous spectra.
The method extends Residual Dynamic Mode Decomposition (ResDMD) by explicitly minimizing a spectral residual loss function. The minimisation of the spectral residual contributes in avoiding spectral pollution, where the discretisation of the infinite dimensional operator to a finite matrix results in the discovery of spurious eigenvalues that are numerical artifacts.
The main contributions of this submission is using a feedforward neural network to automatically select the dictionary functions, overcoming the limitations imposed by predefined basis dictionaries used in the approximation of the operator, and using the spectral residual loss in the optimisation.
Through minimising the spectral residual, ResKoopNet aims to approximate both discrete and continuous spectra.
Numerical results demonstrate ResKoopNet's accuracy on several example systems: on a classical pendulum system, on a turbulent flow, and on neural dynamics from mouse visual cortex.
For the pendulum system the proposed approach is shown to outperform existing methods in approximating the Koopman operator in terms of the number of basis functions (observables) required for accurate spectrum approximation (proposed method seems to require much fewer basis functions compared to ResDMD for same amount of data ) .
Claims And Evidence: The authors claim that ResKoopNet addresses the spectral inclusion and spectral pollution issues of previous Koopman approximation methods. For the pendulum system the authors demonstrate that the method effectively tackles the spectral pollution issue and the spectral inclusion by increasing the number of observables.
Methods And Evaluation Criteria: - The use of spectral residual as a loss function is conceptually valid and justified given existing literature, making it suitable for evaluating the accuracy of spectral approximation of the operator.
- The choice of the pendulum system as a benchmark makes absolutely sense, because the method can be compared against ground truth. However the same is not true for the other two benchmarks. For the turbulent flow experiment I am not entirely convinced that the method outperforms competing methods (see my questions below), while regarding the neural data experiment I am not sure about the motivation of applying the method in this setting.
- However, more explicit justification for choosing specific hyperparameters (e.g. the size and structure of neural networks, number of eigenfunctions, and dimensionality reductions) would be beneficial. See also my questions below.
Theoretical Claims: I checked the derivations in A.2 and A.3
Experimental Designs Or Analyses: Yes I checked the presented experiences and I have included some of my issues and comments also in the other comments
Regarding the experiment with the application on neural data:
- I am not sure why the authors choose to compare their method and the competing method in Figure 6A using a different number of eigenfunction (500 vs 50). In A9 the authors justify partly their choice, but I would expect to see how their method performs with 50 basis functions to compare it to Hankel-DMD, and to see in the main text a comparison with a competing methods with the same number of functions. Since the constraint for the Hankel-DMD and the kernel ResDMD is the number of snapshots I would expect first to see a comparison of all methods with this number of bases, and then additionally present results with more bases where possible. Thus, I am not entirely convinced about the validity of the remaining analyses performed on this dataset, but I remain open to being persuaded otherwise by the authors.
Supplementary Material: Yes, A.7, A.1, A.4, A.2, A.3, A.5,A.8, A.9
Relation To Broader Scientific Literature: The method builds upon extensive literature on data-driven approximation of dynamical systems, and in particular on data-driven approximation of the Koopman operator. Specifically it extends recent work that uses the spectral residual to clear the identified spectral eigenpairs from spurious eigenpairs introduced through the numerical approximation of the infinite operator. It extends the existing literature by first using a neural network as a dictionary of observables/basis functions instead of using pre-selected basis, and uses the spectral residual as a loss function. Existing DMD methods optimise the dictionary of active basis function in the approximation by including a L1 cost on the basis coefficients.
Essential References Not Discussed: I am not aware of any, but I do not word directly in this sub-field.
Other Strengths And Weaknesses: **Strengths:**
- Identifies Koopman operator by directly optimising the error of the approximation of the operator in the eigenspace
- Can approximate the operator for systems with continuous spectra, unlike EDMD-like approaches
**Weaknesses:**
- As mentioned by the authors the method is sensitive to hyperparameter selection.
- The writing and organising of the text could benefit from a bit of restructuring. For instance, the reference to the pseudospectrum in page 4 should be in my view under a separate subsection. Also when describing the experiments, the reader needs sometimes more background details to understand the setting. E.g. when describing the turbulent example the reader has to go to the paper of Colbrook &
Townsend (2024) to understand the experimental setting.
- High computational demands discussed in A.5, but it is acceptable as first implementation of the approach that can be improved on in follow-up work
Other Comments Or Suggestions: - Page 5: the authors write " Even with a much larger amount of dataset": I think they want to write amount of datapoints"
- the fonts in most figures are too small to be readable.
- In Fig. 5, since you are trying to relate the 2D pressure field of the original system to the first eigenfunction of the learned Koopman operator, I would suggest to rescale the colormaps so that the associated regions in the two upper plots have same/similar colouring. (minor)
Questions For Authors: - For the high dimensional turbulent system, do you reduce first the dimensionality of the state with SVD, and then compute the Koopman approximation? If yes, how do you select the reduced dimensionality? Can you show a plot with the singular values? Do you follow the same procedure for all methods?
- For the turbulent flow experiment, in the paper of Colbrook &Townsend (2024), the authors show both for DMD and ResDMD that the eigenfunctions have some characteristic details indicative of the acoustic sources. In the plots you provide in the main text from the proposed method, and in the appendix from the Hankel-DMD these details are absent. As a non-specialist, I wonder why this is the case, and whether you can still claim successful approximation of the operator, when such details are not captured by the proposed method.
- Related to the previous question, throughout the high dimensional experiments the authors seem to select to first reduce the dimensionality of the data to 300 through SVD and then apply the method. How do you select that value?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: 1. We would like to thank the reviewer for the helpful comments. The updated figures and proof can be seen here: https://anonymous.4open.science/r/rebuttal_materials-14918/
2. Regarding the benchmarking question:
(1) In the 2nd experiment, the 300 basis functions we have chosen are indeed different from the 250 basis functions used in the original ResDMD paper (Colbrook & Townsend, 2024). We have re-done the experiment and the results are shown in **Fig5_new.png**;
(2) In the neural experiment, to fairly compare with the 50 bases used in Hankel-DMD, we re-estimated the Koopman eigenfunctions using 50 dictionaries (24 SVD-truncated bases, one constant, and 25 trainable bases). The performance remained comparable to the case with 501 bases. See **Fig_6_new.png and Fig_13.png, Fig_16.png** for the averaged eigenfunctions and clustering results.
We would like to clarify that the results are robust to hyperparameter choice (hidden layer number and neuron size in the hidden layer) when they reach a threshold for a given dataset. To illustrate this, we have added a hyperparameter scan result in **Fig_8.png** by scanning the hidden layer size from 1 to 4 and each layer’s neuron size in the range of [250, 275, 300, 325, 350]. The figure shows that the performance is robust with the increase of both hyperparameters, suggesting that varying the layer size will not trigger sensitive changes in the approximation results after a certain threshold. Similar robustness results are shown for the neural experiment in **Fig_17.png**: with smaller layer size and layer number, the clustering performance is not stable but becomes robust after the two hyperparameters reach a threshold. This justifies our network structure of 3 layers of 200 neurons.
3. We agree that the topic of “pseudospectrum” should be separated. We can put it at the bottom of Section 3.1 with the title “Continuous Spectra and Pseudospectrum”.
4. We will add some background details for turbulence example: ‘The turbulent flow dataset from Colbrook & Townsend (2024, Section 6.3) models a two-dimensional airfoil system with Reynolds number $3.88 \times 10^5$ and Mach number $0.07$. The data captures a pressure field at 295,122 spatial points across 798 time steps, sampled every $2 \times 10^{-5}$ seconds’.
5. We will extend the computational cost analysis and incorporate computational bottlenecks and theoretical extensions.
6. The colormap values of all Koopman modes in **Fig5_new.png** now have the same scale.
7. In the turbulence experiment, we will add further explanation of how truncated SVD is applied before using ResKoopNet. We applied a change of basis method here; specifically, consider the data matrix decomposed by truncated SVD $X=USV^\top$ with truncation $k=150$ singular values, then multiplying $V$ on both sides from the right to get $XV=US$, which is the lower dimensional data matrix projected by matrix $V$; then we apply ResKoopNet and compute its (low-dimensional) Koopman modes; then multiply the matrix $V^\top$ from the left to recover the original Koopman modes. Koopman modes and eigenfunctions are ranked by ascending spectral residuals, where smaller residuals indicate better approximations.
8. We added singular value plots in Figures 5(e) and (f) (see **Fig5_new.png**), revealing a significantly large singular value corresponding to the dominant spatial pattern captured by Koopman mode 1 in Figure 5(b).
9. Yes, we used SVD for both high-dimensional experiments(2nd and 3rd). In the turbulence example, we chose the 150 reduced dimension following Colbrook & Townsend, 2024. In the neural example, we reduce the data into 300 dimensions as it is a manageable dimension compared to the original dimension (>7000), but thanks to the reviewer we have demonstrated that with a smaller truncated dimension (24) we also get meaningful eigenfunctions (see previous reply). We also use the same method (filtered by spectral residual) in selecting eigenvalues in 1st pendulum experiment, selecting Koopman modes in 2nd turbulence experiment, and selecting eigenfunctions in 3rd neural experiment.
10. In **Fig5_new.png (c)(d)**, we have also illustrated the acoustic vibration and turbulent fluctuation characteristics. The original Hankel-DMD results in Appendix Figure 7 are similar to Figure 5(c)(d) and those in the ResDMD paper, which has no new characteristic to specify.
11. Regarding the SVD procedure: we first reduced spatial dimension to 150 using truncated SVD. Then, we applied ResKoopNet to obtain 1+150+149=300 Koopman modes ranked by ascending spectral residual. Here, '1' denotes a constant non-trainable basis, '150' are SVD-reduced spatial coordinates, and '149' are trainable bases (later adjusted to '99' for a total of 250 to match the original ResDMD setup). We then selected the less "polluted" (low-dimensional) Koopman modes and mapped them back to the original high-dimensional space using the SVD matrix $V$.
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Rebuttal Comment 1.1:
Comment: I thank the authors for their detailed reply to my comments (and to the comments of the other reviewers). Their responses have sufficiently addressed my concerns and I appreciate the additional effort they put in to clarify our concerns and improve their work. Therefore I will update my evaluation accordingly.
However, I expect the authors to incorporate the suggested edits/clarifications that resulted from the reviews into their manuscript/supplement, since these details clarify their work and improve reproducibility.
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Reply to Comment 1.1.1:
Comment: Thank you very much for your kind feedback and suggestion. I truly appreciate your time and comments, which have helped improve the clarity and quality of the work. While ICML did not allow manuscript updates during the rebuttal phase, I have incorporated all suggested edits and clarification into the updated version of the paper to ensure better reproducibility. | null | null | null | null | null | null |
Dialogue Without Limits: Constant-Sized KV Caches for Extended Response in LLMs | Accept (poster) | Summary: The authors consider the problem of maintaining a fixed size KV cache during autoregressive generation with large language models. The key idea is to retain recent tokens and a limited number of old tokens according to a dynamic selection algorithm that uses the attention patterns of future tokens on past tokens. Morph KV achieves similar performance compared to strong baselines while using a significantly smaller KV cache size.
Claims And Evidence: The claims are well supported by extensive experiments. morph KV maintains a smaller KV cache than prior methods while retaining what seems like good performance as measured by LM judge scores, completion rates, and accuracy on benchmarks like long gen bench.
This is more of a presentation note but it seems like this notion of of selection bias during decoding hinders methods like H2O but I'm not totally clear what the selection bias is or how it was evaluated, at least in a more explicit way
Some of the baselines felt a bit like red herrings. For example, Snap KV is obviously not a good fit for long-form generation, although I appreciate that there might not be other good long-form generation KV cache techniques
Methods And Evaluation Criteria: The authors use standard long generation benchmarks. Regarding long-form generation quality I'm not necessarily super convinced by LM judge scores so it would have been better to have a human evaluation but I realize this is tricky. One question I have is why was H2O not compared against in the long bench tasks in experiment 5.3? Is it because H2O maintains too large of a KV cache?
Theoretical Claims: NA
Experimental Designs Or Analyses: I checked the soundness of all experiments, they seem reasonable and standard benchmark/baselines. I would have liked to see the prompt used for the LM judge and maybe some discussion of whether or not there's a standard prompt or LM judge framework like alpaca eval for long form generation.
Supplementary Material: No
Relation To Broader Scientific Literature: I think the discussion of prior methods is clear although I'm not totally clear on some of the design choices of these baselines with respect to this work. for example for H2O, why isn't there a hyperparameter that can help you reduce the number of retained KVs?
Essential References Not Discussed: Regarding clarity I thought the math notation was Overkill in section 3.1.3 I mean basically you're looking at the sum of attention weights or the max attention weight over some window from recent tokens. I think the other presentation issue was that the problem statement for finding a reduced cache size was good but it's not clear how the local coherence or distant relative heuristics really optimize that objective or approximate that objective in any meaningful way.
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: Regarding clarity I thought the math notation was Overkill in section 3.1.3 I mean basically you're looking at the sum of attention weights or the max attention weight over some window from recent tokens. I think the other presentation issue was that the problem statement for finding a reduced cache size was good but it's not clear how the local coherence or distant relative heuristics really optimize that objective or approximate that objective in any meaningful way.
Beyond the heuristics you've proposed in this paper for defining notions of what KV entries are important do you have any adversarial examples of when these heuristics miss out tokens are actually important?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback. We have addressed the points raised in the review below:
**Q-1) Selection Bias in H$_2$O**
R-1) H$_2$O retains tokens based on aggregated attention scores. This introduces a selection bias because it retains early tokens even when they do not significantly attend to newer tokens. Various prior works, like NACL [1], Keyformer, and EMS [2], have made similar observations. In NACL, the authors extensively study this problem using LongBench tasks on the Llama-2-7B model. While generating the last token, 96% of H$_2$O’s KV cache comprises entries from the first 200 tokens, while only 4% is derived from the subsequent 1199 tokens. Please refer to the NACL paper (particularly **Figure 2 (a)**) for details about this study.
[1] NACL: https://aclanthology.org/2024.acl-long.428.pdf
[2] EMS: https://arxiv.org/pdf/2412.08521
**Q-2) SnapKV for Long-Form Generation**
R-2) Indeed, SnapKV’s overwhelming memory requirements make it unsuitable for long-response tasks. While H$_2$O is more memory-efficient for these tasks, its performance is limited due to the problem of selection bias towards early tokens. MorphKV efficiently navigates this trade-off and achieves robust performance and high memory efficiency for both long-context and long-response tasks.
**Q-3) H$_2$O for Long-Context Benchmarks**
R-3) SnapKV is the state of the art for long-context tasks and already outperforms H$_2$O [1]. Hence, we only compare against SnapKV because outperforming it naturally implies outperforming H$_2$O (please see **Section-5.3** of their paper).
[1] SnapKV: https://proceedings.neurips.cc/paper_files/paper/2024/hash/28ab418242603e0f7323e54185d19bde-Abstract-Conference.html
**Q-4) Prompt for LM Judge**
R-4) We use the publicly available LongWriter framework in our studies. LongWriter uses a single-answer grading approach, where an LLM judge is asked to assign a score to a single answer (please refer to Section 3.1 in [1] for further details). The prompt used for the LM judge can be found here: https://github.com/THUDM/LongWriter/blob/main/evaluation/judge.txt
[1] Judging LLM-as-a-Judge with MT-Bench and Chatbot Arena: https://arxiv.org/abs/2306.05685
**Q-5) Design Choices in H$_2$O Baseline**
R-5) The performance of a KV cache pruning method depends on the quality of the retained KVs and how these are utilized for future tokens. In contrast, the memory savings depend on the number of KVs evicted. Naively reducing the memory capacity of H$_2$O also lowers its performance due to the limited accuracy of its token selection policy that exhibits a bias toward preserving early tokens (please see our earlier response).
Our studies using LongGenBench on the Mistral-24B-Instruct model show that MorphKV has 1.67$\times$ better accuracy when both H$_2$O and MorphKV operate within the same cache budget. To achieve comparable accuracy for the same task, H$_2$O must overcome the limitations of its token selection policy and retain a lot more KVs, increasing the memory footprint. MorphKV is 3.6$\times$ more memory-efficient compared to H$_2$O in this case.
**Q-6) Local coherence and Distant Relative Heuristics in MorphKV**
R-6) Local and distant heuristics enable MorphKV to capture useful information. Discarding recent tokens severely degrades performance, critical to maintaining the text’s local coherence. In contrast, distant heuristics are crucial to generating an apt response overall, as they capture information that establishes the global pre-text and relevance.
MorphKV leverages the insight that due to transformers’ auto-regressive nature of output token generation, each token attends to all its past tokens and naturally holds awareness of the useful distant tokens. MorphKV retains only those distant tokens identified as relevant by preceding recent tokens, allowing the current output token to focus solely on this curated set of useful distant tokens.
**Q-7) Adversarial Cases where Heuristics Overlook Important Tokens**
R-7) The ability to retain *useful* or *important* distant tokens depends on the accuracy of the heuristics and the choice of the appropriate design hyperparameters. For example, the default implementation of MorphKV uses a window size of 32 because it works well across most representative tasks. However, for certain benchmarks that involve recalling information over very long time spans, such as LongGenBench, while this window size captures *most* of the useful distant tokens, the performance can be improved slightly by increasing the window size (which would allow capturing all useful distant tokens). Please see **Table-3** and **Table-4** in response to **Reviewer bnHA** for the detailed results. However, the probability of encountering such scenarios is very low because we carefully tune them, and the most appropriate window size can be well approximated based on the nature of the task and its information span. | Summary: The authors introduce MorphKV, a KV cache compression method for large language models (LLMs). MorphKV is an inference-time technique that maintains a fixed-size KV cache in autoregressive Transformers, addressing the issue of memory expansion as sequence length increases. Unlike traditional approaches that rely on truncation or lossy compression, MorphKV employs a correlation-aware selection mechanism to dynamically prioritize tokens, ensuring high-fidelity context retention while mitigating early-token bias. By continuously refining the KV cache based on recent attention patterns, MorphKV surpasses state-of-the-art methods such as SnapKV, achieving 86.5% memory savings and 13.5% higher accuracy. This makes it particularly effective for long-form tasks like content creation and code generation, enhancing the efficiency of LLM deployment in real-world applications.
Claims And Evidence: The paper validates its claim of **constant-size KV cache inference while preserving performance** through benchmark results.
However, beyond overall scores, there is little supporting evidence. The authors do not provide theoretical or empirical justification for why MorphKV should outperforms existing KV compression methods.
Additionally, since the KV cache size is a hyperparameter, it is unclear how to determine its optimal value in practice while ensuring performance preservation.
Methods And Evaluation Criteria: The evaluation criteria overall make sense.
However, I found that the full attention model performs worse than KV cache pruning methods, including MorphKV, in LongWriter and LongGenBench. The authors do not provide sufficient explanation for these abnormal results. (In contrast, in LongBench, one of the most widely used benchmarks, the full attention model maintains top performance.)
The paper primarily presents overall benchmark performances, which does not help in gaining a fine-grained understanding of the method. For better clarity, the authors could include example-level or task-level (e.g., retrieval, reasoning) analyses to offer deeper insights into their approach.
Theoretical Claims: The paper does not contain theoretical claims.
Experimental Designs Or Analyses: Please check Methods And Evaluation Criteria above.
Supplementary Material: Yes. I've checked experimental results.
Relation To Broader Scientific Literature: This paper's evaluation is limited to NLP, but the inference algorithm could also be applied to Transformer models in other domains.
Essential References Not Discussed: I do not find any essential references that need discussion.
Other Strengths And Weaknesses: Strengths
- The paper is generally easy to read.
- The paper is self-contained.
Weaknesses
- [**Important**] The paper does not include an analysis of inference time. A key issue is that the proposed method is not compatible with fused attention kernels, such as FlashAttention, since it requires attention scores at each decoding step, which are unavailable for fused kernels.
- The approach appears to be a combination of SnapKV (prefilling phase) and H2O (decoding phase). I find little novelty or new insights in the proposed method.
Other Comments Or Suggestions: In Figure 3, it appears the authors have **misunderstood the H2O baseline**. This method dynamically evicts tokens from the KV cache during generation, rather than retaining all early tokens. As presented, Figure 3 is misleading. (For reference, please see their paper: https://arxiv.org/pdf/2306.14048)
Questions For Authors: - Could you provide statistical testing on LongWriter and LongGenBench? I am not convinced that the full attention model performs worse than KV cache pruning methods. I suspect there may be significant variance in performance.
- Is MorphKV compatible with FlashAttention?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback.
**Q-1) Comparison with Prior Works**
R-1) MorphKV’s superior performance mainly stems from its more accurate token selection policy.
StreamingLLM retains the KVs of the first few initial tokens called *attention sinks* and a sliding window of tokens, evicting all intermediate tokens between them. This creates a “context gap”, leading to partial capture of distant context as noted by prior works [1]. In contrast, MorphKV retains distant tokens (including important intermediate tokens) actively attended by recent tokens, enabling essential context capture throughout token generation.
MorphKV eliminates the token selection bias dominant in H$_2$O and Keyformer. MorphKV exploits the insight that due to the auto-regressive nature of token generation, each token attends to all its past tokens and thus, is naturally aware of useful distant tokens. MorphKV retains only those distant tokens identified as relevant by preceding recent tokens, allowing the current output token to focus only on a curated set of useful distant tokens.
SnapKV assumes that critical tokens from the input prompt remain critical throughout token generation. Based on this insight, it does not prune the KV cache during token generation. However, LLMs often suffer from *degeneration* while generating large responses [2] as each token attends to all past tokens, compounding noise from early decoding steps. As SnapKV retains KVs of all generated tokens, it is significantly more vulnerable to degeneration and performance degradation for long-response tasks. In contrast, MorphKV only retains *important* tokens in the KV cache enabling it to generate more coherent responses.
Degeneration is quantified using the rate at which phrases are repeated in the LLM response. **Table-9** shows that SnapKV has 1.3$\times$ higher repetition rate than MorphKV on LongWriter.
### **Table 9**: Text Degeneration via N-Gram Repetition
|Llama3.1-8B-Instruct|MorphKV|SnapKV|Full-Attention|
|-|-|-|-|
|Repetition Rate|68%|89%|89%|
[1] Attention-Gate: https://arxiv.org/pdf/2410.12876
[2] Text Degeneration: https://arxiv.org/abs/1904.09751
**Q-2) Why MorphKV outperforms Full-Attention (FA)**
R-2) Although we intuitively expect FA to perform superior to KV cache pruning techniques, for the same reasons as described above (degeneration), it may actually perform worse for certain tasks. Recent works, like SnapKV, and PyramidKV also make similar observations. SnapKV argues that FA often introduces noise to the attention mechanism by retaining all tokens, hindering its ability to attend to only the most relevant tokens more strongly. This trend is heavily task-dependent and KV cache compression does not always guarantee outperforming full-attention. For example, while MorphKV outperforms FA for few long-response tasks, FA outperforms MorphKV by 1.8% on LongGenBench for Qwen2.5-32B-Instruct.
**Q-3) Statistical testing**
R-3) Our results do not exhibit any statistical variance because MorphKV performs greedy decoding, and therefore generated responses remain same across runs.
**Q-4) Optimal Value of KV cache size**
R-4) We can obtain the optimal values through Grid-Search with validation on the end task. For our evaluations, we perform a coarse-grained search and determine that a KV cache size of 4K tokens is a practical starting point for most tasks.
**Q-5) Generalizability of MorphKV**
R-5) Please refer to **R-4** in response to **Reviewer vs1e**.
**Q-6) Inference Time**
R-6) Please refer to **R-5** in response to **Reviewer Jsuc**.
**Q-7) Comparison of MorphKV against combination of SnapKV and H$_2$O**
R-7) MorphKV differs substantially from a naive combination of SnapKV and H$_2$O. This primarily stems from the token selection policy used in MorphKV. Although both H$_2$O and MorphKV prune the KV cache dynamically during the decode phase, they use different policies to identify the *important* KVs they must retain. Consequently, even for the same memory budget, the set of KVs retained by the two approaches is significantly different. Please refer to R-1 for a detailed discussion regarding how MorphKV compares with SnapKV.
**Q-8) H$_2$O Illustration**
R-8) We use Figure 3 only as an illustrative example to highlight that H$_2$O’s token retention policy introduces a bias towards early tokens due to aggregated attention scores, similar to *Figure 2 (a)* in NACL [1]. We will update the figure to highlight the dynamic token-eviction in H$_2$O.
[1] NACL: https://arxiv.org/pdf/2408.03675
**Q-9) Compatibility with FlashAttention**
R-9) Yes, MorphKV is already compatible with FlashAttention (please see **Section 4** of the paper). While fused kernels do not provide attention scores directly, It is still possible to tweak the FlashAttention kernel to return partial attention matrices alongside the final attention output, which can be consumed by MorphKV. An in-depth discussion of this is beyond the focus of this work.
---
Rebuttal Comment 1.1:
Comment: I appreciate the detailed rebuttal! I understand your point regarding the H2O description. To avoid confusion and clearly convey the message, I hope the authors update the figure.
Regarding Table 9, which is informative, more fine-grained analyses that provide insights into the working mechanisms of the proposed methods would be valuable for improving the paper.
Regarding fused attention, you might use FlashAttention alongside but fusing your method inside the fused algorithm is not trivial, as the FlashAttention kernel does not calculate partial attention matrices. It only maintains blocks of **output** features, which are recurrently updated using the partial **unnormalized attention score** (no softmax over entire keys) and scaling factors. Storing the full attention score per query token in GPU SRAM is infeasible for long-context, so your approach might decrease FlashAttention performance even if integrated. There are studies highlighting post-training compression methods do not achieve theoretical improvements in real-world applications due to a lack of hardware awareness [1].
Despite these limitations, the authors have clarified my questions, so I have updated my score to weak reject.
[1] Yuan et al., Native Sparse Attention: Hardware-Aligned and Natively Trainable Sparse Attention, 2025
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for their thoughtful follow-up and updated score. We will revise our manuscript to include Table 9. We are in the process of developing a modified FlashAttention kernel in Triton. MorphKV mitigates storage overhead by using attention profiles only from recent window tokens. However, as even these may exceed SRAM capacity, we offload partial unnormalized attention blocks to HBM, albeit at the cost of increased memory bandwidth.
We thoroughly appreciate the comments related to fused kernels and will highlight the associated challenges and trade-offs in the final version of our paper. | Summary: This paper introduces **MorphKV**, a method that dynamically selects caching tokens in pre-trained language models during inference. Unlike prior approaches such as **streamingLLM** and **SnapKV**, MorphKV employs two metrics—*sum fusion* and *max fusion*—to identify and retain tokens most closely attended to by recent tokens during both the **prefill** and **decoding** stages. By leveraging this dynamic caching strategy, MorphKV effectively supports generation tasks involving long contexts and extended responses.
Claims And Evidence: The paper is well-written, and most of the claims are supported by evidence.
In lines 381-384, “this suggests that larger models can better leverage MorphKV…” seems to be not supported by existing experiments.
Methods And Evaluation Criteria: Standard benchmark like LongBench is utilized in the paper for evaluation. Also proposed a long-response scenario for evaluation.
Theoretical Claims: Not applicable.
Experimental Designs Or Analyses: In the paper, the author conducted experiments in both long response and long context scenarios.
Supplementary Material: I have reviewed the written supplementary material. In the appendix, the authors conducted an additional ablation study regarding Sum/Max Fusion and Local window size.
Relation To Broader Scientific Literature: In the paper, there are two major concepts that are prefilled token selection and decode token selection. For prefil,l it is closely related to SnapKV, while MorphKV utilizes slightly different metrics. For decode head, it is more closely related to H2O.
Essential References Not Discussed: Not applicable
Other Strengths And Weaknesses: ### Strengths
1. MorphKV addresses an important challenge in LLM inference, particularly relevant to scenarios involving long-context processing and long-response generation.
2. The paper is well-organized, clearly written, and easy to follow.
### Weaknesses
1. The largest model evaluated in the experiments is Phi-4 (14B parameters). The authors' claim in lines 381–384 that "larger models can better leverage MorphKV" is speculative and not sufficiently supported by their current experimental results.
2. MorphKV appears to be a relatively minor modification to existing caching methods. The novelty could be better highlighted by clearly differentiating it from previous methods, such as streamingLLM and SnapKV.
3. Long-context and long-response generation present distinct caching challenges. The paper lacks detailed analysis or justification for why these particular tasks are the most appropriate to demonstrate the efficacy of the proposed strategy.
Other Comments Or Suggestions: N/A.
Questions For Authors: 1. In the Appendix, only an ablation regarding the number of recent tokens and fusion strategy is presented. Do you expect performance differences when varying the total number of cached tokens beyond just recent tokens?
2. Dynamically selecting tokens for caching appears computationally expensive. Could you clarify whether this is indeed the case? If so, could you provide runtime comparisons between MorphKV, SnapKV, and H2O?
3. Previous methods typically retain older tokens and their all associated information (i.e., full column). In MorphKV, are initial tokens progressively evicted as generation length increases? If tokens are evicted, could this negatively impact performance in tasks that heavily rely on information retrieval?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback. We have addressed the points raised in the review below:
**Q-1) Analysis on Larger Models**
R1) MorphKV remains effective for larger models, as demonstrated by our recent evaluations with larger models. We request the reviewer consult **Table-1** and **Table-2** in the response to **Reviewer fibk**.
**Q-2) Comparison with Prior Works**
R2) For a detailed comparison with prior works, including StreamingLLM and SnapKV, please refer to **R-1** in response to **Reviewer-FtVG**.
**Q-3) Choice of Benchmarks**
R-3) Both long-context and long-response generation tasks cater to widely prevalent applications of LLMS and are key areas of focus [1-3]. Long-context generation not only represents common use cases of LLMs like text summarization and passage retrieval but can also be used for innovative training techniques such as multi-shot learning, where the model can learn from hundreds of training examples provided directly in the prompt.
In contrast, long-response generation is crucial for tasks such as story generation, paragraph completion, comprehensive question-answering, content creation, etc. While prior works, such as SnapKV, are optimized explicitly for long-context tasks, they are inefficient for long-response tasks. MorphKV addresses this critical bottleneck.
[1] Google: https://cloud.google.com/transform/the-prompt-what-are-long-context-windows-and-why-do-they-matter
[2] IBM: https://research.ibm.com/blog/larger-context-window
[3] Amazon: https://aws.amazon.com/blogs/security/context-window-overflow-breaking-the-barrier/
**Q-4) Effect of KV cache budget on MorphKV**
R-4) Thanks for the detailed feedback. We have conducted additional studies using LongGenBench tasks for the Mistral-24B-Instruct [1] model to evaluate the impact of varying cache capacities on performance. We observe that the performance of both MorphKV and H$_2$O increases with the number of cached tokens. At the same KV cache capacity, MorphKV remains more effective than H$_2$O. We will revise the Appendix to include these results.
### **Table 7**: Performance with increasing KV cache capacity on LongGenBench
|KV cache compression method (number of cached tokens) |Completion Rate|Average Accuracy|
|-|-|-|
|H$_2$O (1000) | 56.46% | 35.0%|
|H$_2$O (2000) | 61.35% | 52.0%|
|H$_2$O (4000) | 61.35% | 58.4%|
|MorphKV (1000) | 61.64% | 40.0%|
|MorphKV (2000) | 61.64% | 54.0%|
|MorphKV (4000) | 61.64% | 58.4%|
[1] Mistral-24B-Instruct: https://mistral.ai/news/mistral-small-3
**Q-5) Is dynamic token selection for caching computationally expensive? If so, how does the runtime of MorphKV compare to SnapKV and H$_2$O?**
R-5) KV cache compression methods must navigate complex trade-offs encompassing accuracy, inference time, throughput, and memory footprint. Optimizing for a single metric alone is insufficient for practical adoption.
MorphKV prunes the cache at every token processing step, which increases the computational overhead. Our implementation employs several optimizations to reduce these overheads, such as CPU offloading and prefetching with dedicated CUDA streams that minimize the time overhead associated with loading attention weights.
Compared to a similar dynamic token eviction policy, such as H$_2$O, MorphKV achieves **8%** faster inference time (while remaining more accurate). MorphKV’s runtime is higher than SnapKV’s, which is expected because SnapKV is tailored for long-context tasks, not long-response ones.
However, the reduced memory footprint of the KV caches enables MorphKV to deliver a much higher throughput (up to 4.68$\times$) due to a larger batch size, effectively compensating for the degradation observed in the runtime of each request. In conclusion, MorphKV outperforms existing KV cache compression techniques by achieving the best overall balance: it reduces KV cache memory usage by up to 85%, increases throughput by 4.68$\times$, and achieves an inference time improvement of 8% over state-of-the-art methods (such as H$_2$O) – all while preserving or improving accuracy. **Table 8** summarizes these results.
### **Table 8**: Comparison of key metrics across KV cache compression methods for Mistral-7B on LongBench
|Task|SnapKV|H$_2$O|MorphKV|
|-|-|-|-|
| Runtime | 1$\times$ | 1.62$\times$ | 1.50$\times$ |
| Throughput | 1$\times$ | 2.4$\times$ | 4.68$\times$ |
| Accuracy | 1$\times$ | 0.94$\times$ | 1.01$\times$ |
| Memory | 1$\times$ | 0.26$\times$ | 0.14$\times$ |
**Q-6) MorphKV on Retrieval Tasks**
R-6) MorphKV dynamically evicts tokens based on attention weight scores of the recent window tokens. Hence, it is not biased towards retention or eviction of initial tokens during generation. We evaluate MorphKV on the LongBench suite, which includes many retrieval tasks (single-doc QA, multi-doc QA, Passage Retrieval etc.), and MorphKV shows robust performance across all these tasks.
---
Rebuttal Comment 1.1:
Comment: I would like to thank the authors for their detailed rebuttal! Their supplementary results have further demonstrated the effectiveness of the algorithm! I will stand with my current score.
---
Reply to Comment 1.1.1:
Comment: We sincerely appreciate the reviewer’s time and positive feedback. Thank you for acknowledging our supplementary results and for your support! | Summary: The paper introduces MorphKV, a novel method for efficiently managing key-value (KV) caches in Large Language Models (LLMs) while maintaining memory efficiency and model accuracy. The method overcomes the problem of growing memory requirements for KV caches during inference by employing a dynamic, correlation-aware token selection process. MorphKV reduces memory usage by up to 88.1%, providing higher accuracy and scalability compared to current state-of-the-art methods such as SnapKV and H2O.
Claims And Evidence: MorphKV claims to offer substantial improvements in both memory efficiency and model performance. Through experimental evaluations on various LLMs (e.g., Llama, Mistral, Qwen), the authors show that MorphKV achieves 86.5% memory savings with a 13.5% increase in accuracy over previous methods. These results are demonstrated across multiple benchmarks, including long-response generation and long-context understanding tasks.
Methods And Evaluation Criteria: The authors evaluate MorphKV's performance on tasks such as long-response generation (LongWriter), long-context understanding (LongBench), and structured long-response tasks (LongGenBench). These tasks are compared to SnapKV and H2O, using key metrics like model accuracy, KV cache sizes, and task completion rates. The method's memory efficiency is also tested under varying response lengths, with MorphKV demonstrating stability even as outputs grow larger.
Theoretical Claims: The paper introduces the theory that the selective retention of KV tokens based on correlation with recent tokens helps to preserve long-range dependencies while minimizing memory usage. This claim is supported by the experimental results, where MorphKV's selective KV cache management outperforms prior methods that either discard or retain uncorrelated tokens.
Experimental Designs Or Analyses: The experimental design includes comparative studies using different state-of-the-art methods for KV cache compression. The results indicate that MorphKV performs favorably in both memory efficiency and task accuracy. The experiments are robust, spanning a variety of LLMs and task categories, and also consider different fusion strategies (sum and max fusion) for selecting KV tokens.
Supplementary Material: The paper includes detailed supplementary material, including tables comparing the performance of MorphKV with H2O and SnapKV across various models and tasks. Additional comparisons of fusion strategies provide insight into the sensitivity of MorphKV to window size and memory budgets.
Relation To Broader Scientific Literature: The work builds on existing research in KV cache compression for LLMs, extending previous approaches like SnapKV, H2O, and Keyformer. By dynamically selecting relevant tokens, MorphKV advances these methods, offering better scalability and efficiency. The authors also relate their findings to memory management strategies in other machine learning models and systems.
Essential References Not Discussed: While the paper cites numerous relevant works, it could have explored more recent advancements in KV cache optimization and memory-efficient model architectures. For example, methods that combine KV cache compression with layer-specific optimizations might provide additional insights for further improvements. (i.e. PyramidKV, Ada-KV, HeadKV)
Other Strengths And Weaknesses: Strengths: The paper proposes a practical, real-time solution for LLM inference tasks that need memory efficiency without sacrificing performance. MorphKV's ability to scale with response length is a notable advantage for tasks involving extended outputs, which are increasingly common in applications like content generation and interactive assistants.
Weaknesses: The paper could have benefited from more detailed discussions on the potential trade-offs between the computational complexity of the token selection process and its memory efficiency. The impact of MorphKV on inference speed is not discussed in detail, which could be a critical factor in real-time applications.
Other Comments Or Suggestions: Further work could explore the integration of MorphKV with other model architectures, particularly those that focus on multi-modal data. The efficiency of MorphKV could also be tested on more specialized benchmarks, such as those involving medical or legal text generation, to assess its generalizability across domains. Additionally, future versions could investigate the computational overhead introduced by the dynamic KV cache selection process.
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their appreciation of our work. We have addressed the point raised in the review below:
**Q-1) Paper Could Explore PyramidKV, Ada-KV, HeadKV Advancements**
R-1) Thank you for the excellent suggestion. MorphKV is orthogonal to methods like PyramidKV, which optimizes the KV cache across layers, and Ada-KV and Head-KV, which optimize the KV cache across attention heads. Thus, integrating MorphKV with these methods can improve its efficacy even further. In fact, we have already conducted some preliminary studies wherein we simulate a layer-wise optimization by naively deactivating MorphKV for the first three layers based on prior studies that describe the importance of information in the early layers [1,2,3]. Our studies show that this design is even more effective (with roughly 10% additional memory requirements) than the default implementation of MorphKV, which prunes the KV cache uniformly across all model layers. The results are summarized in **Table 5** below.
Integrating MorphKV with methods like PyramidKV, Ada-KV, and Head-KV as a generalized solution requires a deeper understanding of how the methods complement each other, careful tuning of the design parameters, and development of a robust policy that dynamically combines them for optimal performance. Such an extensive study is beyond the scope of our current paper, and we reserve it for future work.
### **Table 5**: MorphKV with basic layer-wise optimization for Mistral-7B on LongGenBench
|Task|Completion Rate|Average Accuracy|
|-|-|-|
|MorphKV (default) | 70.51 | 44.2%|
|MorphKV (layer-wise optimization) | 71.96 (2.05% better) | 46.1% (4.29% better)|
MorphKV configuration has a capacity of 2000 tokens
[1] PyramidKV: https://arxiv.org/pdf/2406.02069
[2] SqueezeAttention: https://openreview.net/forum?id=9HK2rHNAhd
[3] Layer-condensed KV cache: https://aclanthology.org/2024.acl-long.602.pdf
**Q-2) Trade-Off between Computational Complexity and Memory Efficiency**
R-2) By default, MorphKV prunes the KV cache after each token is processed to attain a constant-sized cache, which incurs additional computational overheads. The overheads can indeed be lowered by adopting a *lazy* token-selection policy, at the cost of slight performance degradation. The computational savings scale in the number of pruning steps skipped by the lazy token-selection policy. For example, if MorphKV prunes the cache after every 10 tokens processed, the computational overheads reduce to 0.1$\times$ of that required in the default MorphKV.
To study this further, we implement a variant of MorphKV, which allows the KV cache to exceed the pre-allocated capacity before pruning it back. **Table 6** compares the performance of the default and lazy variant of MorphKV. We will include these results in the revised manuscript.
### **Table 6**: MorphKV with lazy token-selection for Mistral-7B on LongGenBench
|Task|Completion Rate|Average Accuracy|Runtime|
|-|-|-|-|
|MorphKV (default) | 72.10 | 47.0%|1$\times$|
|MorphKV (with lazy token-selection) | 71.86 (0.34% worse) |46.1% (1.9% worse)|0.82$\times$|
MorphKV configuration has a capacity of 4000 tokens
**Q-3) Inference Time**
R-3) We request the reviewer to consult R-5 in response to **Reviewer Jsuc**.
**Q-4) Generalizability of MorphKV**
R-4) We already evaluate MorphKV using the LongBench [1] suite that encompasses tasks such as question answering [2,3] based on academic, legal, government, literature and financial reports, reasoning [4-6] from articles and reports from wikipedia, and summarization [7] on documents from academia and product development (please see **Section-5.3**). MorphKV delivers robust performance across these tasks, showing its generalizability across various domains
[1] LongBench: https://arxiv.org/pdf/2308.14508
[2] NarrativeQA: https://ar5iv.labs.arxiv.org/html/1712.07040
[3] Qasper: https://paperswithcode.com/dataset/qasper
[4] HotpotQA: https://paperswithcode.com/dataset/hotpotqa
[5] 2wikiMQA: https://aclanthology.org/2020.coling-main.580/
[6] PassageCount: https://arxiv.org/pdf/2308.14508
[7] QMSum, VCsum: https://arxiv.org/pdf/2308.14508 | Summary: This work designed and developed an efficient KV cache management technique to keep constant KV size while achieving higher accuracy for long context and long response tasks. The author has compared with relevant works, e.g., SnapKV, H2O and full attention, etc, using different model and different benchmarks comprehensively. The evaluation shows that MorphKV achieved start of art performance on KV size controlling and benchmark task accuracy.
Claims And Evidence: Yes. The claims and evidence are clear and well backed by numbers and detailed step by step illustration.
Methods And Evaluation Criteria: Yes. The method makes sense to the problem, i.e., keeping relevant context in the older tokens is helpful for the performance.
The evaluation process is comprehensive, i.e., different models and benchmarks are evaluated to compare MorphKV with existing works.
Theoretical Claims: Yes, the theory and math are correct. The key part is to calculate the attention weights, which makes sense and seems correct.
Experimental Designs Or Analyses: Yes. The experimental design and analysis are done on a H200 with NVLink.
Supplementary Material: Yes, I have reviewed the appendix. The last part caught my attention, i.e., the window size is a parameter that impacts the performance of MorphKV, which indicates that the system may be hard to be adopted by real world system.
Relation To Broader Scientific Literature: Yes. The key contribution of this paper is it identified a better attention mechanism related to the coherence and semantic meaning of all the tokens, i.e., history token and recent token. Such that, more research can be inspired from this work on how to retain older tokens for better performance and optimized KV cache management.
Essential References Not Discussed: Yes.
Other Strengths And Weaknesses: NA
Other Comments Or Suggestions: NA
Questions For Authors: How easy to use in real world system.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback. We have addressed the points raised in the review below:
**Q-1) Effect of Window Size on MorphKV**
R-1) The window size indeed affects the performance of MorphKV. In practice, **all** KV cache pruning methods rely on hyperparameters: examples include total cache capacity in H$_2$O and Keyformer, window sizes in StreamingLLM and SnapKV, and the number of layers for KV cache projection in SwiftKV. Careful tuning of these parameters is essential for practical adoption and achieving substantial memory savings [1,2].
Similarly, MorphKV also benefits from tuning its window size parameter. Our experiments show that a window size of 32 consistently offers high performance across all LongBench suite tasks, including diverse scenarios such as code generation and literature review. Although increasing window sizes can slightly improve performance for tasks requiring information recall over longer spans, it typically yields diminishing returns, as described in **Table 3** and **Table 4**. Hence, the window size can be coarsely approximated based on the nature of the task in terms of the information span to achieve good performance.
### **Table 3**: Mistral-24B-Instruct performance on LongGenBench
| MorphKV Configuration | Completion Rate | Average Accuracy |
|:--:|:--:|:--:|
| window size: 32 | 61.55% | 54.3% |
| window size: 200 | 61.64% | 58.4% |
### **Table 4**: Qwen2.5-32B-Instruct performance on LongGenBench
| MorphKV Configuration | Completion Rate | Average Accuracy |
|:--:|:--:|:--:|
| window size: 32 | 71.68% | 51% |
| window size: 200 | 71.68% | 53% |
NOTE: each scenario above has a total KV cache capacity of 4000 tokens
[1] Accelerating Enterprise LLM Workloads: https://www.snowflake.com/en/engineering-blog/swiftkv-llm-compute-reduction/
[2] StreamingLLM Integration into TensorRT-LLM: https://github.com/NVIDIA/TensorRT-LLM/tree/main/examples/llama#run-llama-with-streamingllm
**Q-2) Ease of Usage in Real-World Systems**
R-2) Currently, MorphKV is implemented in the widely used transformers library from HuggingFace (see **setup in Section-4**). MorphKV is integrated inside both standard Attention and FlashAttention modules and uses cache offloading to accommodate demanding memory-intensive use cases. Consequently, MorphKV is compatible with a vast spectrum of models hosted on HuggingFace. Our approach is consistent with prior works and facilitates seamless adoption across LLMs for real-world scenarios. | Summary: This paper presents MorphKV to reduce the KV cache in long LLM context. Its dynamic KV selection algorithm improves the accuracy by 18.6 and 13.6 compared to previous SnapKV and H2o, while reducing KV by 88.1 and 51.6.
## update after rebuttal
During the rebuttal, the authors add experiments on larger (24B, 32B) to demonstrate the effectiveness of the method. Though I did not further increase my score (my initial score is 4), I am very supportive of the proposed methods and paper.
Claims And Evidence: The paper claims to achieve lower KV cache usage and higher accuracy, which is well supported by Table 1 and Figure 6.
Methods And Evaluation Criteria: Yes, it runs on llama3-8b, Mistral-7b, qwen-7b, phi 14b which are leading LLMs. It evaluates on LongWriter, LongBench; it compares against SnapKV and H2o, which all make sense.
Theoretical Claims: There are no theoretical claims.
Experimental Designs Or Analyses: The experimental designs make sense. It evaluates against the two baselines and the above mentioned LLMs and benchmarks. It shows the method reduces the KV cache size with improved accuracy.
Supplementary Material: Yes, the reviewer mainly review for Appendix A and B.
Relation To Broader Scientific Literature: Related work in compressing KV are either not scalable or has limited accuracy (as discussed in the background section). This paper introduces a scalable method with high accuracy after KV compression.
Essential References Not Discussed: The paper discusses the majority of related works.
Other Strengths And Weaknesses: The paper is well written, and the results are significant.
Other Comments Or Suggestions: I am wondering whether the author can include more analysis on larger models. The current models are 7-14B, where the efficiency issue in larger models is more severe. However, the reviewer votes for accept due to the clear effectiveness of the method.
Questions For Authors: Please see the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's feedback on both the structure of our paper and the results. We have addressed the points raised in the review below:
**Q-1) Analysis on Larger Models**
R-1) MorphKV remains effective even for larger models. We evaluate MorphKV using long-response tasks from the LongGenBench suite on an Nvidia H100 GPU equipped with 80 GB of HBM-2e memory on two models (Mistral-24B-Instruct [1] and Qwen2.5-32B-Instruct [2]). Even for a single task, SnapKV consumes significant KV cache sizes: 6.16 GB (50.26 GB including weights) and 9.7 GB (71.14 GB including weights), respectively, nearly exhausting the GPU's available HBM capacity. In contrast, MorphKV requires only 0.80 GB and 1.06 GB, respectively. The tables below summarize these results. The evaluated model sizes are consistent with prior works, like SnapKV (7B), H$_2$O (30B), and Keyformer (7B).
### **Table-1**: Mistral-24B-Instruct on LongGenBench
| KV Cache Compression Method | Completion Rate | Average Accuracy | KV cache size |
|:--:|:--:|:--:|:--:|
| SnapKV | 61.40% | 57.8% | 7$\times$ |
| H$_2$O | 61.35% | 58.4% | 3.6$\times$ |
| **MorphKV** | **61.64%** | **58.4%** | **1$\times$** |
### **Table-2**: Qwen2.5-32B-Instruct on LongGenBench
| KV Cache Compression Method | Completion Rate | Average Accuracy | KV cache size |
|:--:|:--:|:--:|:--:|
| SnapKV | 71.59% | **54%** | 9.1$\times$ |
| H$_2$O | 71.39% | 53% | 4.6$\times$ |
| **MorphKV** | **71.68%** | 53% | **1$\times$** |
[1] Mistral-24B-Instruct: https://mistral.ai/news/mistral-small-3
[2] Qwen2.5-32B-Instruct: https://qwenlm.github.io/blog/qwen2.5/
---
Rebuttal Comment 1.1:
Comment: Thank you for getting back! I maintain my score and support this paper.
---
Reply to Comment 1.1.1:
Comment: Thank you so much for supporting our paper! We sincerely appreciate your time and thoughtful feedback in reviewing it. | null | null |
Tree-Sliced Wasserstein Distance: A Geometric Perspective | Accept (poster) | Summary: The paper introduces a novel approach to **projected Optimal Transport (OT) computation**, termed **Tree-Sliced Wasserstein (TSW) Distance**. The key contributions include:
1. **Tree Systems**, a generalization of straight-line projections that incorporate hierarchical structures.
2. **Radon Transform on Tree Systems**, along with its **injectivity property**, ensuring meaningful projections.
3. **Tree-Sliced Wasserstein Distance**, which retains a **closed-form solution** and satisfies **metric properties** for OT computation.
# update after rebuttal
Most of my concerns have been explained, and I raised my score to 3 (weak accept).
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The paper presents several key **theoretical claims** that establish the foundation of **Tree-Sliced Wasserstein (TSW) Distance**:
- **System of Lines (Definition 3.1)**: Introduces a **set of $k$ lines**, referred to as a **system of lines**, which forms the basis for tree-based projections.
- **Tree Structure Construction (Algorithm 1)**: Provides a **procedure for constructing tree systems**, ensuring connectivity and well-defined hierarchical structures.
- **Radon Transform on Systems of Lines (Definition 4.1) & Injectivity (Theorem 4.2)**:
- Defines a **Radon Transform** adapted to tree systems.
- Proves **injectivity**, ensuring that distributions mapped onto tree systems retain distinct information.
- **Tree-Sliced Wasserstein Distance (Definition 5.1) & Metric Property (Theorem 5.2)**:
- Formalizes **TSW distance** as an extension of Sliced Wasserstein using tree projections.
- Establishes **metric properties**, proving that TSW is a **valid distance function** for probability measures.
Experimental Designs Or Analyses: Yes, I've reviewed the experiment designs and analyses.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: ### **Relation to Prior Work**
Classical **Optimal Transport (OT)** methods project data onto a **single straight line**, as seen in the **Sliced Wasserstein (SW) Distance** and its variants. The proposed **Tree-Sliced Wasserstein (TSW) Distance** generalizes this by **projecting data onto a system of $k$ lines**, forming a hierarchical structure that better preserves geometric and topological properties.
#### **Related References**
1. **Carriere et al. (2017) [1]** – Introduced the **Sliced Wasserstein Kernel** for persistence diagrams, leveraging one-dimensional projections to improve OT computations.
2. **Liutkus et al. (2019) [2]** – Proposed **Sliced-Wasserstein Flows**, using 1D projections for generative modeling, demonstrating the efficiency of SW-based transport.
3. **Kolouri et al. (2019) [3]** – Developed **Generalized Sliced Wasserstein Distances**, modifying the projection mechanism but still relying on **one-dimensional lines**.
The **TSW approach extends these works** by incorporating **multi-line tree-based projections**, which retain computational efficiency while improving structure preservation.
Essential References Not Discussed: Recommend to add the following:
[1] Carriere, M., Cuturi, M., & Oudot, S. (2017). Sliced Wasserstein kernel for persistence diagrams. *In ICML 2017 - Thirty-fourth International Conference on Machine Learning*, pp. 1–10.
[3] Kolouri, S., Nadjahi, K., & Simsekli, U. (2019). Generalized Sliced Wasserstein Distances. *Advances in Neural Information Processing Systems (NeurIPS)*.
Other Strengths And Weaknesses: ## Weaknesses
1. **Unclear tree structure/tree topology**
- One of the key concepts of tree structure and tree topology is not clearly explained. See Question 1 for details.
2. **Combination of Tree Random Transform (Eq. 9) and Closed-Form Wasserstein Tree Distance (Eq. 13)**
- The tree-sliced Wasserstein distance appears to project data into the union of joint line segments, where the first and last line segments have infinite length, and all other middle line segments have finite length.
- If this understanding is correct, I do not see why this slicing approach retains more information than simply projecting onto these \( k \) lines.
- Specifically, suppose each line system \( \mathcal{L} \) contains \( k \) lines. I cannot see how the projected tree Wasserstein distance in \( \mathcal{L} \) contains more information than the standard sliced Wasserstein distance projected onto these same \( k \) lines, given that their computational costs are identical.
3. **Dependency on the tree construction algorithm (Algorithm 1)**
- The performance of the tree Wasserstein distance seems to heavily rely on the tree construction method.
- In particular, choosing \( x_1 \sim [-1,1] \) and \( t_i \sim [-1,1] \) may not always be optimal, especially when the data scale is too large or too small.
- I recommend that the authors discuss the potential impact of these hidden hyperparameters and explore a grid search strategy to optimize them.
4. **Limitations in extending to \( L^2 \) cost**
- The tree Wasserstein metric appears to be difficult to extend to \( L^2 \) cost due to the constraints of the tree metric structure.
- In contrast, the classical sliced Wasserstein (SW) distance can naturally incorporate an \( L^2 \) cost.
- The authors should discuss this limitation in detail and consider potential ways to address it.
Other Comments Or Suggestions: N/A
Questions For Authors: ## 1. P3, Line 127
- **Sentence unclear:** *"quotient at the intersection of these copies."* Could the authors clarify this statement?
- **(1.1) Quotient space clarification:**
Given a set \(X\) and an equivalence relation \(\sim\), the quotient space \(X/\sim\) consists of the disjoint union of all equivalence classes in \(X\) determined by \(\sim\). I recommend including a simple example to illustrate the concepts of equivalence relation and equivalence class in this context.
- **(1.2) Defining the tree structure in higher dimensions:**
If \(d \geq 3\), then, in general (with probability 1), randomly selected lines \((x^1, l^1)\) and \((x^2, l^2)\) do not intersect. In this case, how is the tree structure defined? Additionally, if such a scenario occurs, how is the tree distance in Equation (6) determined?
- **(1.3) Understanding Figure 1:**
I find Figure 1 difficult to interpret. The caption states that *"only four pairs of lines are adjacent."* I assume the authors mean pairs \((1,3), (1,4), (1,5), (2,4)\). However, intersections also occur for \((2,3), (2,5), (2,1), (3,4), (3,5), (4,5)\). Could the authors clarify why these additional intersections on the left are not counted as adjacent nodes in the tree structure?
## 2. P4, Line 252
- The statement *"We can show \( R_L^\alpha f \in L^1(L) \)"* appears inconsistent. However, in Equation (9), the domain of \( R_L^\alpha f \) is \( \tilde{L} = (\mathbb{R}^d \times L) \), not \( L \). Could the authors clarify this?
## 3. Experiment 6.2
- **(3.1) Missing baselines:**
- I recommend adding "generalized sliced Wasserstein" as a baseline in at least one experiment.
- Additionally, I suggest including the \( L^2 \) cost for "SW" as a baseline. Furthermore, for a fair comparison, always set \( L(SW) = L(TSW) \times k(TSW) \).
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Answer W2.** All the lines in a tree system are infinitely long. In practical applications, empirical measures have bounded support. As a result, when these measures are projected onto the lines of a tree system, the resulting measure on the tree system also has bounded support.
*It is worth noting that TSW-SL is a more general framework than SW [...] in any prior sliced Wasserstein variant, as those methods operate strictly with single-line projections in each slice*. (Kindly refer to Answer **Q1 + Q2** in our response to Reviewer 8fkW for the full details)
**Answer W3.** In practical applications, we aim to position the tree root and sources in proximity to the empirical data. Therefore, as noted in line 320, “the tree systems will be sampled such that the root is positioned near the mean of the target distribution,” i.e., near the data mean. We simply write the distribution of $x_i, t_i$ as stated to emphasize that the sampling process naturally induces a distribution over the space of trees.
We thank the Reviewer for suggesting a grid search strategy to optimize the sampling method. However, we consider this beyond the scope of the current paper and view it as a promising direction for future work. This is analogous to how SW was initially developed with randomly sampled lines, and subsequent works later refined the sampling process for improved performance.
**Answer W4 + Q3.** For $p>1$, the proposed approach can be extended. However, the Tree-Wasserstein distance with $p>1$ lacks a simple closed-form approximation (see [1]). A meaningful alternative is provided by Sobolev Transport [2], which offers a closed-form approximation and has been applied in the tree-sliced framework, as discussed in Eq. (13).
Although we do not mention the case of $p >1$ in the paper, our implementations support arbitrary values of $p$. Indeed, all experiments in the paper are conducted with $p=2$, as it serves as the default setting. We believe this way of writing simplifies the presentation by avoiding the complexities of the Sobolev Transport literature, while still preserving flexibility in implementation. For this reason, we have chosen not to include it in our paper.
Due to space constraints, we strongly encourage the Reviewer to refer to the Sobolev Transport literature. Our extension to the $p>1$ case still satisfies the theoretical guarantees discussed in the paper.
**Answer Q1.** The full tree system concept requires rigorous derivation, that is why we emphasize that Section 3 offers only an intuitive and concise overview, and a careful reading of Appendix A is necessary for full mathematical rigor. While some notations may seem redundant at first glance, they are ultimately essential for defining the concepts precisely.
**(1.1)** The sentence mentioned in Section 3.2 is mathematically correct, with a rigorous explanation in Appendix A.3.
As the Reviewer suggested, we can visualize the system of two lines as follows: Let $l$ and $l'$ be two lines that intersect at a point $x$. The points $(x,l)$ of $l$ and $(x,l')$ of $l'$ — representing the same point $x \in \mathbb{R}^d$— are identified. By taking the quotient topology, the resulting tree system formed from $l$ and $l'$ resembles the shape of the letter "X".
**(1.2)** The Reviewer may have missed the connectedness condition noted in line 153. A tree system is formed only when the set of lines is connected—a property we define rigorously in Appendices A.1 and A.2. Overlooking this condition may also contribute to the confusion in the following discussion.
**(1.3)** In Fig. 1, when viewed as lines in $\mathbb{R}^2$, the five lines intersect pairwise, making the system connected. Once connected, a tree structure can be imposed by selecting only four adjacent pairs, removing certain geometric intersections. This results in a tree structure where some lines still intersect in space but are not connected in the tree.
This also justifies our use of the notation $(x,l)$ for a point on a line, rather than simply $x$.
**Answer Q2.** We acknowledge that a clarification on an abuse of notation is indeed missing. For simplicity, we denote a function
$f \in L^1(\mathcal{L})$ as a function defined on the ground set of $\mathcal{L}$, denoted by
$\bar{\mathcal{L}}$. We will clarify it.
**Answer Q3.** We kindly refer the Reviewer to the section **Experiments with GSW** in our response to Reviewer 8fkW’s comments.
---
We thank the Reviewer for the constructive feedback, as well as for pointing out typos and missing references, which we will address. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
---
*References.*
[1] Tam Le et al., Tree-Sliced Variants of Wasserstein Distances. NeurIPS 2019
[2] Tam Le et al., Sobolev Transport: A Scalable Metric for Probability Measures with Graph Metrics. AISTATS 2022 | Summary: This paper presents a new variant of the sliced Wasserstein distance, called the tree-sliced Wasserstein distance on systems of lines, or TSW-SL. The main idea is that instead of iteratively projecting the distributions to a random line and computing the average of these 1D Wasserstein distances (as is done in the sliced Wasserstein distance), one can construct a set of randomly selected lines such that each line $\ell_i$ intersects the lines $\ell_{i-1}$. The algorithm then uses a splitter to project the mass of each point to these lines, and then solves the tree Wasserstein distance on these projections efficiently.
## update after rebuttal
I keep my positive score.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes, the theoretical claims are reasonable and the proofs that I checked are correct.
Experimental Designs Or Analyses: Although the experimental setup and evaluation are informative, I believe there is a lack of comparison with more recent methods. As the authors mentioned, their proposed method is an alternative of SW by proposing the system of lines and they do not expect their method to out-perform recent variants of SW, but I think it would be important to have such comparison.
Supplementary Material: I reviewed some of the proofs and the additional experiments.
Relation To Broader Scientific Literature: The sliced Wasserstein distances and its improved variants have been used in numerous contexts in the machine learning domain. This paper also presents a variant of the sliced Wasserstein distance, which improves the performance generative models such as GANs and diffusion models when trained using TSW-SL instead of SW.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Strengths**
The paper presents a new perspective on the sliced Wasserstein distances and presents interesting novel ideas.
**Weaknesses**
Other Comments Or Suggestions: * Line 82 RC: supports repeated
* Line 205 LC: it seems like the two sentences are the same sentence with different wordings
* The definition of $\mathcal{P}$ is given in line 241 RC but is used before that.
* Section 5 and subsection 5.1 have the same title.
Questions For Authors: * Is it true that your algorithm generates a 1D Wasserstein problem instance? More specifically, your algorithm generates a set of line segments connected together, and projects the distributions over these line segments. So although the general framework works for trees, your algorithm only deals with 1D instances. If I understood correctly, would it be more accurate to use a name other than tree-sliced Wasserstein?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1. Is it true that your algorithm generates a 1D Wasserstein problem instance? ... If I understood correctly, would it be more accurate to use a name other than tree-sliced Wasserstein?**
**Answer Q1.** In the Sliced Wasserstein (SW) framework, each line projection leads to a 1D Optimal Transport (OT) problem. Similarly, in our framework, each tree system projection results in an OT problem defined on a tree metric space—specifically, the tree system itself. When the tree system consists of a single line, the resulting OT problem is identical to that of the SW framework.
This highlights that our algorithm extends beyond solving a single 1D OT problem—it handles a collection of OT problems on tree metric spaces. Therefore, we believe the naming of our framework is accurate. In the literature (e.g., [1]), the term Tree-Sliced Wasserstein often refers to approaches where different metrics are sampled to compute the final result. In contrast, our method samples different tree structures (i.e., systems of lines), leading to a fundamentally different construction. Moreover, [1] is applied in a different context and to different types of tasks, making the two approaches inherently non-comparable.
This is precisely why we append “on systems of lines” to our framework’s name—to clearly distinguish it from existing lines of work. To the best of our knowledge, our TSW-SL is currently the only tree-sliced framework that can be effectively applied to large-scale generative tasks involving the transportation of a training measure to a target measure in Euclidean space. Other works on Tree-Sliced Wasserstein (TSW), such as [1], are mainly designed for classification, regression, or clustering tasks and are not applicable to generative settings. This limitation stems from their reliance on clustering-based or nearest-neighbor search frameworks for computing slices—a strategy that is theoretically unsuitable (as the clustering must be recomputed each time the training measure is updated, rendering previous clustering results irrelevant) and empirically inefficient (since clustering is significantly more computationally expensive than linear projection methods).
---
**Experimental Designs Or Analyses.** Although the experimental setup and evaluation are informative, I believe there is a lack of comparison with more recent methods. As the authors mentioned, their proposed method is an alternative of SW by proposing the system of lines and they do not expect their method to out-perform recent variants of SW, but I think it would be important to have such comparison.
**Answer.** For the diffusion task, we were unable to include GSW due to time constraints. However, we would like to highlight the promising potential of our tree-sliced approach. We adopt the same experimental setup as in a recent work on SW [2]. The best performance reported in [2] is $2.70$, compared to $2.90$ from the vanilla SW method. Our approach, TSW-SL, achieves a score of $2.83$.
Our method serves as a foundational replacement for the SW framework, introducing a tree-based structure rather than focusing on optimizing specific components like the sampling method, as done in [2]. Therefore, we do not anticipate a significant performance boost. Nonetheless, because our work establishes a solid foundation, a recent follow-up study (see [3]) that builds upon one instance of our tree-based framework (they use concurent-lines tree structures) has achieved a performance of $2.53$ on the same diffusion task. This result highlights the potential and promising direction of future research in tree-sliced approaches.
In addition, in the Gradient Flow task presented in our paper, we compared our method with several recent sliced Wasserstein (SW) baselines. We also kindly refer the Reviewer to the section **Experiments with GSW** in our response to Reviewer 8fkW’s comments, where we compare TSW-SL with GSW [4] used in Variational Autoencoder.
We appreciate your comment regarding the inclusion of recent SW methods in our paper and will make the necessary revisions accordingly.
---
We thank the Reviewer for the constructive feedback and for pointing out the typos in our paper. We will address them accordingly. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
---
*References.*
[1] Le, T., Yamada, M., Fukumizu, K., & Cuturi, M. Tree-sliced variants of Wasserstein distances. NeurIPS, 2019.
[2] Khai Nguyen et al., Sliced Wasserstein with Random-Path Projecting Directions. ICML 2024.
[3] Hoang Tran et al., Distance-Based Tree-Sliced Wasserstein Distance. ICLR, 2025.
[4] Kolouri, S. et al., Generalized Sliced Wasserstein Distances. NeurIPS, 2019.
---
Rebuttal Comment 1.1:
Comment: I thank the reviewers for their thorough response. I keep my positive score.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer e1vF,
We sincerely appreciate the time and effort you invested in reviewing our submission. Your thoughtful and constructive feedback has been incredibly valuable in helping us improve the quality and clarity of our work.
Thank you once again for your insightful comments and for contributing to the refinement of our research.
Best regards,
Authors | Summary: The authors study the sliced-Wasserstein distance and propose replace projecting measures onto one-dimensional lines with a more complex structure, which they call a tree system. They propose a novel variant of Radon transforms for tree systems which leads to an efficient metric which they call Tree-Sliced Wasserstein on Systems of Lines (TSW-SL). The time complexity to compute TSW-SL is $O(Lkn\log n + Lkdn)$, where $L$ is the number of tree systems sampled, $k$ is the number of lines, and $n$ is the number of projections on each line. Finally, the authors conduct experiments showing the effectiveness of TSW-SL on (1) the gradient flow task where the TSW-SL is better able to minimize Wasserstein distance between a target and source distribution than standard SW distance, (2) GANs where the TSW-SL is used in the adversarial loss term and (3) de-noising diffusion models.
### Update after rebuttal
Thanks to the authors for their response. I maintain my score.
Claims And Evidence: The authors claim that given a system of lines $\mathcal{L}$, one can produce a chain-like tree structure. This tree structure induces a metric on the space induced by the system of lines $\mathcal{L}$, $\Gamma_\mathcal{L}$ -- the space of the disjoint union of copies of $\mathbb{R}$ with their intersections quotiented out. One can then take several systems of lines, $\mathcal{L}_1, \dots, \mathcal{L}_k$, and use their Radon transform on systems of lines to compute their tree-Wasserstein distance on systems of lines. Additionally, this TSW-SL is a proper metric between probability measures. All claims are well supported and I did not see anything problematic.
Methods And Evaluation Criteria: The benchmark datasets and tasks that the authors use are standard for evaluation of SW distances. There are couple of datasets that perhaps the authors could add to their flow minimization experiments, perhaps MNIST so we can see the performance of TSW-SL on a more realistic dataset. Another interesting realistic benchmark/task that the authors could consider is alignment of multi-modal RNA seq datasets, especially because their high-dimensional Gaussian dataset samples distributions over $\mathbb{R}^{200}$ and RNAseq data tends to be inherently much higher-dimensional.
Theoretical Claims: All proofs are in the supplement and I did not check them.
Experimental Designs Or Analyses: I looked through all experiments. I think the gradient flows experiments could be expanded as currently, these experiments are only done with synthetic datasets (Gaussians and Swiss Roll). I think in [KNSBR '19], they do similar experiments and include MNIST to show the performance of GSW on a more realistic dataset. It would be nice to see the performance of TSW-SL under similar conditions. Additionally, I think that there are several variants of sliced-Wasserstein distance (e.g. GSW and correspondingly, max-GSW) and it would be nice to see how TSW-SL compares to GSW.
"Generalized Sliced Wasserstein Distances" [KNSBR '19]
Supplementary Material: I did not review the supplement.
Relation To Broader Scientific Literature: I am not very familiar with the sliced-Wasserstein distance literature. However, to the best of my knowledge, this falls along the same line of work as [WSBOR '13], [KTOR '16], and [KNSBR '19]. While [KNSBR '19] already considered replacing the linear projection in standard sliced-Wasserstein distance with non-linear projections, this paper explicitly projects measures onto tree structures. Once the measures are projected onto tree structures, the computation of OT on trees is also well known from [IT '03] along with a large body of follow-up work on using tree structure to approximate OT.
"A Linear Optimal Transportation Framework for Quantifying and Visualizing Variations in Sets of Images" [WSBOR '13]
"A continuous linear optimal transport approach for pattern analysis in image datasets" [KTOR '16]
"Generalized sliced-Wasserstein distance" [KNSBR '19]
"Fast image retrieval via embeddings" [IT '03]
Essential References Not Discussed: I do not know of any essential references which are not discussed.
Other Strengths And Weaknesses: Strengths: The authors introduce a new framework for sliced Wasserstein distance which uses projection to systems of lines and uses the associated tree structure on the system of lines to compute an efficient metric between measures. I like that this paper connects sliced-Wasserstein distance to tree-Wasserstein distance, which like 1D OT, is another special case where Wasserstein distance can be quickly computed. At least, it is a new framework for sliced-Wasserstein distance which leverages previous work on tree Wasserstein distance. I feel it is somewhat similar in spirit to the sliced-tree-Wasserstein distance [LYFC '19] as in both cases one samples several different trees and then averages the Wasserstein distance between measures in the tree space.
Weaknesses: The authors do cite the generalized sliced Wasserstein distance and they briefly mention in their experiments that they will only compare to vanilla sliced-Wasserstein distance. However, I think either (a) the authors should include a comparison to GSW and max-GSW in their experiments or (b) they should provide more justification as to why they do not compare to GSW. I will elaborate more in the questions/suggestions section.
Other Comments Or Suggestions: I did not immediately see any typos.
Questions For Authors: 1. Can you elaborate more on why you only compare to SW distance? I think it is not very compelling to just say that TSW-SL is just a simple version of SW distance. In that case, it is unclear the utility of TSW-SL in practice when GSW and max-GSW exist.
2. Could you comment on the connection, if any, between GSW and TSW-SL? It seems that there is a generalized Radon transform also defined in GSW.
3. Is it possible to compare (at least in the gradient flow experiment with the swiss roll and Gaussian datasets) to regular sliced tree-Wasserstein distance? It seems that TSW-SL is very similar (in practice) to the sliced tree-Wasserstein distance as in both cases, one samples a collection of trees and then computes the Wasserstein distance between the two measures on the trees.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Answer Q1+Q2.** It appears that the Reviewer may have misunderstood certain key aspects of our paper, as several important points seem to have been overlooked.
Respectfully, we do not claim that TSW-SL is a simplified version of the sliced Wasserstein (SW) distance. On the contrary, TSW-SL is a more general framework than SW. In fact, SW can be seen as a special case of TSW-SL when the underlying tree system consists of only a single line.
This generalization stems from the novel splitting mechanism, denoted by $\alpha$, which is not present in traditional sliced approaches. Instead of projecting the entire mass of a point $x$ onto a single line and computing the 1D Wasserstein distance for each slice, our method allows $\alpha$ to split the mass of $x$ across multiple projections—each corresponding to a line in the tree system. The Wasserstein distance is then computed over this richer tree structure. This is the key reason that TSW-SL serves as a non-trivial generalization of SW.
To the best of our knowledge, such a mechanism does not exist in any prior sliced Wasserstein variant, as those methods operate strictly with single-line projections in each slice.
Finally, there is no direct connection between GSW and TSW-SL due to a fundamental difference in their formulations: TSW-SL is defined over tree systems, whereas GSW operates within the line setting.
**Answer Q3.** To the best of our knowledge, our TSW-SL is currently the only tree-sliced framework that can be effectively applied to large-scale generative tasks involving the transportation of a training measure to a target measure in Euclidean space. Other works on Tree-Sliced Wasserstein (TSW), such as [1], [2], [3], are mainly designed for classification, regression, or clustering tasks and are not applicable to generative settings. This limitation stems from their reliance on clustering-based or nearest-neighbor search frameworks for computing slices—a strategy that is theoretically unsuitable (as the clustering must be recomputed each time the training measure is updated, **rendering previous clustering results irrelevant**) and empirically inefficient (since clustering is significantly more computationally expensive than linear projection methods).
We did not include these methods as baselines because applying them in our generative setting is *infeasible*.
**Experiments with GSW.** All the tables are provided in: https://sites.google.com/view/tree-sliced-wasserstein-distan.
*Gradient Flow.* We included GSW as a baseline to evaluate alongside our methods on the gradient flow task using the 25 Gaussians dataset. As shown in Table 4, TSW-SL consistently outperforms both maxGSW and GSW (circular). While GSW (homogeneous-polynomial) converges faster, TSW-SL slightly surpasses it in performance during the final training epochs.
*Generative modeling.* We further conducted experiments comparing GSWAE and TSWAE on the generative modeling task using MNIST dataset, following the setup from [KNSBR '19]. As reported in Table 5, TSW-SL achieves superior performance over GSW in minimizing the distance between reconstructed samples and the prior, and between the reconstructed samples and the target distributions.
*Denoising diffusion.* We were unable to include GSW in the diffusion task due to time constraints. However, we would like to highlight the promising potential of our tree-sliced approach. For this task, we adopt the same experimental setup as the recent variant of SW in [5]. The best performance reported in [5] is $2.70$, compared to $2.90$ from the vanilla SW method. Our approach, TSW-SL, achieves a score of $2.83$.
Note that, our method serves as a foundational replacement for the SW framework, introducing a tree-based structure rather than focusing on optimizing specific components like the sampling method, as done in [5]. Therefore, we do not anticipate a significant performance boost. Nonetheless, because our work establishes a solid foundation, a recent follow-up study (see [4]) that builds upon one instance of our tree-based framework (they use concurent-lines tree structures) has achieved a performance of $2.53$ on the same diffusion task. This result highlights the potential and promising direction of future research in tree-sliced approaches.
---
We thank the Reviewer for the constructive feedback. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
---
*References.*
[1] Indyk & Thaper. Fast image retrieval via embeddings, 2003.
[2] Backurs et al. Scalable nearest neighbor search for optimal transport. ICML, 2020.
[3] Le et al. Tree-sliced variants of Wasserstein distances. NeurIPS, 2019.
[4] Tran et al. Distance-Based Tree-Sliced Wasserstein Distance. ICLR, 2025.
[5] Nguyen et al. Sliced Wasserstein with Random-Path Projecting Directions. ICML, 2024. | Summary: The paper proposes a novel variant of Sliced Wasserstein (SW) distance, termed Tree-Sliced Wasserstein Distance on Systems of Lines (TSW-SL). The key innovation is replacing one-dimensional projection lines in SW with tree systems, which allow for better preservation of topological structures while maintaining computational efficiency. The authors provide theoretical analysis proving the injectivity of their proposed Radon Transform on Systems of Lines, discuss metric properties, and derive a closed-form solution for OT problems on tree systems. Empirical results demonstrate that TSW-SL improves upon SW in tasks such as gradient flows, generative models, and denoising diffusion models.
Claims And Evidence: The claim that TSW-SL provides a better geometric perspective than SW by capturing more structural information seems insufficient. The role of a system of lines in TSW-SL is analogous to the random projections in SW. In SW, each data point $ a_i $ projects onto $ \theta_i $ via the dot product $ a_i^T \theta_i $, enabling 1D sorting of points within a distribution. However, TSW-SL lacks this sorting property because each data point $ a_i $ is projected onto a line $ l $ based on $ \alpha(a_i)_l $, where $ \alpha $ is a predefined hyperparameter, thereby losing the spatial information of $ a_i $.
For instance, if $ \alpha $ is a constant vector for all data points $ \{a_i\} $, the total mass on each line $ l $ remains exactly $ \alpha_l $ for any probability distribution, making the TSW-SL distance between any two distributions zero. This suggests that the geometric and topological properties of TSW-SL depend primarily on $ \alpha $, which is not a compelling justification for its ability to capture meaningful structural information.
Methods And Evaluation Criteria: The definition and formalization of tree systems are clear and well-structured. The method introduces a novel tree system as an alternative to random projections, differing from classical tree structures such as QuadTree and ClusterTree (although this distinction is not explicitly mentioned in the main text). However, the method appears incomplete, particularly regarding Eq. (13):
1. **Setting the value of $ w_e $**: How should $ w_e $ be determined? For instance, should it be based on the Euclidean distance between $ x_i $ and $ x_{i+1} $? This is not specified.
2. **Defining the root and subtree $ \Gamma(v_e) $**: The statement that "the root is positioned near the mean of the target distribution" is vague. How exactly should the root be set, and what constitutes the subtree $ \Gamma(v_e) $?
3. **Choosing $ \alpha $**: This is the most critical aspect. Given a distribution $ \mu $ with points $ \{a_i\} $ and a distribution $ \nu $ with points $ \{b_j\} $, where $ \{a_i\} $ and $ \{b_j\} $ may differ, how can a universal $ \alpha $ be generated for all these points?
4. **Training $ \alpha $**: It is mentioned that $ \alpha $ can be "a trainable constant vector," but how should it be trained? If it is set as a constant vector for all points, then the total mass on each line $ l $ is exactly $ \alpha_l $, assuming $ \sum_i u_i = 1 $ for probability distributions.
Theoretical Claims: The theoretical derivations appear solid, with proofs provided in the supplementary material. The injectivity of the Radon Transform on Systems of Lines is well-supported. However, offering additional intuition behind certain proofs—such as why tree metrics naturally yield closed-form solutions—would enhance clarity.
Experimental Designs Or Analyses: 1. The experimental setup is reasonable, but the comparisons primarily focus on SW and a few of its variants (MaxSW, SWGG, LCVSW). It would be beneficial to evaluate the method against other tree-Wasserstein distance approaches, such as QuadTree [1], FlowTree [2], and ClusterTree [3], along with their sliced versions.
- [1] Piotr I., Nitin T. *Fast Image Retrieval via Embeddings*, 2003.
- [2] Backurs, A., Dong, Y., Indyk, P., Razenshteyn, I., & Wagner, T. *Scalable Nearest Neighbor Search for Optimal Transport.* ICML, 2020.
- [3] Le, T., Yamada, M., Fukumizu, K., & Cuturi, M. *Tree-Sliced Variants of Wasserstein Distances.* NeurIPS, 2019.
2. The paper lacks a hyperparameter study on the impact of different tree configurations on performance, particularly for the hyperparameters $ k $, $ L $, and $ \alpha $. Although Appendix E.3 provides an ablation study on the number of lines, it only considers values in {$3,4,5$}. A more convincing analysis would explore a broader range, such as $ k = ${$5, 10, 20, 50$}.
- For instance, if $ k $ increases, can $ L $ be reduced while maintaining the same accuracy?
- With a fixed $ L $, does increasing $ k $ improve accuracy?
These relationships remain unclear and would benefit from further investigation.
Supplementary Material: The supplementary material includes detailed theoretical proofs, additional empirical results, and implementation details. The proofs appear rigorous, but some additional insights into the geometric intuition behind tree systems could enhance readability.
Relation To Broader Scientific Literature: The paper effectively situates itself within the broader optimal transport and machine learning literature. It builds upon foundational works on Sliced Wasserstein distances and tree-based OT metrics but could benefit from a more direct comparison with recent tree-Wasserstein approximations.
Essential References Not Discussed: The paper primarily cites literature on SW variants and tree-based metrics but does not discuss more recent developments in tree-Wasserstein methods (e.g., QuadTree [1], FlowTree [2], and ClusterTree [3]).
[1] Piotr Indyk, Nitin Thaper. Fast image retrieval via embeddings, 2003.
[2] Backurs, A., Dong, Y., Indyk, P., Razenshteyn, I., & Wagner, T. Scalable nearest neighbor search for optimal transport. ICML, 2020.
[3] Le, T., Yamada, M., Fukumizu, K., & Cuturi, M. Tree-sliced variants of Wasserstein distances. NeurIPS, 2019.
Other Strengths And Weaknesses: Strengths:
1. Well-motivated theoretical contributions.
2. Empirical validation includes a diverse set of experiments.
3. Computational efficiency is maintained compared to SW.
Weaknesses:
1. The experimental validation primarily focuses on SW and lacks comparisons with broader tree-Wasserstein distance approaches.
2. The connection between tree structures and improved topological preservation needs further clarification. It remains unclear how the tree system captures topological information (see the discussion in the Claims and Evidence section).
3. The study lacks a detailed ablation or hyperparameter analysis on the sensitivity of performance to tree parameters ($k$, $L$, and $\alpha$).
Other Comments Or Suggestions: A small suggestion:
Line 288: The proof for the below theorem is provided in Appendix D.1. → The proof for the theorem below is provided in Appendix D.1.
Questions For Authors: 1. Have you considered alternative tree-Wasserstein distances beyond tree systems, such as QuadTree, FlowTree, and ClusterTree, including their sliced versions? If so, how do they compare?
2. How sensitive is the performance of TSW-SL to the choice of hyperparameters, including $ k $, $ L $, and $ \alpha $? A more detailed ablation study on different tree configurations would be valuable:
- If $ k $ increases, can $ L $ be reduced while maintaining the same accuracy?
- For a fixed $ L $, does increasing $ k $ improve accuracy?
3. How should $ \alpha $ be set for any data points $ a_i $ or $ b_j $? How should $ \alpha $ be trained? If it is set as a constant vector for all points, then the total mass on each line $ l $ is exactly $ \alpha_l $, assuming $ \sum_i u_i = 1 $ for probability distributions.
4. In Line 299, why is TSW-SL identical to SW when $ k = 1 $? In SW, all data points are projected onto a 1D line via the dot product $ a_i^T \theta_i $, resulting in a 1D sorting of points. However, in TSW-SL with $ k = 1 $, all masses $ \{u_i\} $ or $ \{v_i\} $ are projected onto the same line without a sorting relationship. Then, using Eq. (13), the system consists of a single line/edge, and the value of Eq. (13) simplifies to $w_e \cdot \left( \sum_i u_i - \sum_i v_i \right)$. If $ \mu $ and $ \nu $ are probability distributions, then this equals zero. Is this interpretation correct?
5. How is $ w_e $ calculated, and what constitutes the subtree $ \Gamma(v_e) $ in Eq. (13)?
There may be a misunderstanding of Eq. (13), but to be honest, the key steps in calculating the final distance appear to be missing—specifically, the choice of $ \alpha $ and the value of $ w_e $.
I will increase my score if the above concerns are addressed.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Based on the two sections discussed below in the review, it appears the Reviewer may have fundamentally misunderstood our framework. Let us clarify this step by step:
**Claims and Evidence.** The term $\alpha(a_i)_l$ represents the mass allocated to the projection of point $a_i$ onto line $l$, not the location of $a_i$ on line $l$. This misunderstanding seems to be the root of the confusion noted in the review. The second paragraph now does not align logically. Furthermore, our method TSW-SL, similar to SW, involves sorting the projections of data points on each line, as detailed in lines 284-291 of our paper. We have meticulously discussed these concepts in Section 4 where the Radon Transform is defined, and provided explicit formulations in Section 5.2.
**Methods and Evaluation Criteria**.
1. We define the value $w_e$ as the distance between two consecutive points on each line within the tree systems.
2. The terms "root" and "subtree" are used in their typical graph-theoretical sense, while "the root is positioned near the mean of the target distribution" pertains to the sampling method used for the root in our experiments.
3. The same misunderstanding from Claims and Evidence persists: $\alpha$ defines mass distribution across $k$ projections, not their locations.
---
We highly encourage the Reviewer to revisit the paper, as the current review suggests that several key points may have been overlooked. We sincerely appreciate the time and effort put into the review and are especially grateful for its constructive aspects. The foundation of our work is significant, as it serves as the backbone for several other studies—some of which, focusing on special cases of our framework, have already been well-received and published (See [4], [5]).
---
All the tables are provided in: https://sites.google.com/view/tree-sliced-wasserstein-distan.
For **Q3 and Q4**, please refer to the above discussion, as they stem from a misunderstanding.
---
**Answer Q1.** To the best of our knowledge, our TSW-SL is currently the only tree-sliced framework that can be effectively applied to large-scale generative tasks involving the transportation of a training measure to a target measure in Euclidean space. Other works on Tree-Sliced Wasserstein, such as [1], [2], [3] are mainly designed for classification or clustering tasks and are not applicable to generative settings. This limitation stems from their reliance on clustering-based or nearest-neighbor search frameworks for computing slices—a strategy that is theoretically unsuitable (as the clustering must be recomputed each time the training measure is updated, **rendering previous clustering results irrelevant**) and empirically inefficient (since clustering is significantly more computationally expensive than linear projection methods).
We did not include these methods as baselines because applying them in our generative setting is *infeasible*.
While approaches in [3] do not apply to our setting, it provide a closed-form OT solution in tree metrics (see Prop. 1, [3])—crucial for deriving Eq. (13). However, our focus differs fundamentally from [3].
**Answer Q2.** We conducted experiments on the gradient flow task in response to the two scenarios mentioned by the Reviewer.
1. Increasing $k$, reducing $L$: Table 1.
2. Fixing $L$, increasing $k$: Table 2.
Overall, the results show that our method is robust across different $k$ and $L$ values. For a fair comparison, we set $k$ and $L$ so that $N \times k$ matched the total projection directions in SW and its variants.
We also explored fixing $L$ while increasing $k$. As shown in Table 3, this improves performance in GAN tasks. Notably, TSW with total 40 directions outperformed SW with 50, underscoring our method's effectiveness.
**Answer Q5.** Intuitively, given $N$ points in $\mathbb{R}^d$ and a tree system consisting of $k$ lines, the projection results in a total of $kN+k$ points on the tree structure. Specifically, each of the $N$ points gives $k$ projections, contributing $kN$ points, while the additional $k$ points come from the $(k-1)$ intersections among the lines and the root of the tree. These points together form a tree in the graph-theoretic sense. Here, $w_e$ denotes the length of edge $e$ in this tree, and the notion of a subtree follows standard definitions in graph theory. A detailed summary of how a set of points on tree systems forms a tree metric space is presented in Corollary A.12, Appendix A.
---
We thank the Reviewer for the constructive feedback, as well as for pointing out typos and missing references, which we will address. If the Reviewer finds our clarifications satisfactory, we kindly ask you to consider raising the score. We would be happy to address any further concerns during the next stage of the discussion.
---
*References.*
[4] Hoang Tran et al., Distance-Based Tree-Sliced Wasserstein Distance. ICLR 2025
[5] Hoang Tran et al., Spherical Tree-Sliced Wasserstein Distance. ICLR 2025
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed clarification. However, I still have some difficulty fully understanding the algorithm, particularly regarding the definition of the splitting map $\alpha$, the computation of TSW-SL, and the role of the sorting operation. Let me try to clarify my questions more precisely:
- **Splitting map $\alpha$:** I understand that $\alpha(a_i)$ represents the distribution of the mass of point $a_i$ across $L$ lines. In Algorithm 2, $\alpha$ is treated as a hyperparameter, and in Figure 4, it seems that $\alpha$ varies for different points $x$ and $y$. My question is: how is $\alpha$ determined for each point in practice? Is it learned, fixed heuristically, or computed from some geometric property?
- **TSW-SL computation:** Equation (13) follows the standard formulation for computing TWD. Let’s refer to Figure 4, where the two distributions are defined as:
- $\mu$: $f(x) = 0.6$, $f(y) = 0.4$
- $\nu$: $f(x) = 0.4$, $f(y) = 0.6$
Both are supported on the same points $x$ and $y$, with a constant splitting map: $\alpha(x) = \alpha(y) = (1/6, 3/6, 2/6)$.
Now suppose $x_3$ (the intersection of lines 2 and 3) is the root. For edge $e_{23}$ on line 2, the farther endpoint $v_e$ is $x_2$, so the subtree $\Gamma(v_e)$ is rooted at $x_2$. The total mass in this subtree is then:
- For $\mu$: $\alpha(x)_1 \cdot u_x + \alpha(y)_1 \cdot u_y = \frac{1}{6} \cdot 0.6 + \frac{1}{6} \cdot 0.4 = \frac{1}{6}$
- For $\nu$: $\alpha(x)_1 \cdot v_x + \alpha(y)_1 \cdot v_y = \frac{1}{6} \cdot 0.4 + \frac{1}{6} \cdot 0.6 = \frac{1}{6}$
So, the mass difference is zero, and thus the TSW-SL contribution from this edge is zero. Is this interpretation correct? This is what I was trying to ask in the “Methods and Evaluation Criteria – Point 4”.
- **Sorting operation:** I’m unclear about where exactly the sorting operation takes place in Equation (13). Could you kindly clarify which part of the computation involves sorting?
---
*Update:* Thank you for the further clarification. I have increased my score. I hope the authors can include the additional explanation in the main text.
The main confusion I had with the algorithm was in Figure R3 — there is no clear explanation of the edges in the tree in the main text. Initially, I thought Figure 4 only had three edges, so the subtree mass difference for a constant splitting map would always be zero.
The key point is that the projection points must first be sorted along the same line, after which the edges are defined and subtree mass differences are computed. In my example, due to sorting, the TWD is not zero.
In Eq. (13), it should be clarified that the edges $e \in \mathcal{T}$ are based on the sorted projection, not a fixed tree system. Also, since "sorting" only appears in Lines 283 and 286, it would be helpful to explain this more clearly, possibly with a visual.
---
Reply to Comment 1.1.1:
Comment: **Splitting map $\alpha$.** The reviewer is correct in understanding that $\alpha$ represents how the mass of a point is distributed across the $L$ lines. In both Algorithm 2 and Figure 4, $\alpha$ varies depending on the specific point $x$. By definition, $\alpha$ is a function that maps points in $\mathbb{R}^d$ to distributions over lines, and the proposed Radon Transform $\mathcal{R}^\alpha$ depends on how $\alpha$ is initially chosen.
The splitting map $\alpha$ is either set using random vectors or treated as trainable parameters (lines 318-320). In the trainable case, $\alpha$ becomes a constant function, outputting the same vector for all input points. Although this introduces additional parameters compared to the baselines, the number of new parameters is equal to $k$—the number of lines in the tree system—which is small in practice (typically $k \leq 5$).
**TSW-SL computation.** Based on the Reviewer's comments, we provide the following visualization: We start with the two measures $\mu$ and $\nu$ considered by the Reviewer, and use the tree system consisting of three lines as shown in Figure 4. Please refer to the figures provided in https://sites.google.com/view/tree-sliced-wasserstein-distan.
- **Figure R1.** This figure presents the projections of two points, $x$ and $y$, onto the three lines labeled 1, 2, and 3. The projections of $x$ are denoted by $a_i$, and those of $y$ by $b_i$, for $i = 1, 2, 3$.
- **Figure R2.** This figure presents the mass at each projection of $x$ and $y$. For example, the mass at $a_1$ is given by $\mathcal{R}\_\mathcal{L}^\alpha f_\mu(a_1) = f_\mu(x) \cdot \alpha(x)_1 = 0.6 \times 1/6 = 3/30$.
- **Figure R3.** This figure presents the resulting tree after projection. It contains 9 nodes, 6 of which correspond to the projections. The remaining 3 nodes—$x_1$, $x_2$, and $x_3$—come from the default setup of the sampled tree. Specifically, $x_1$ is the root; $x_2$ is the source of line 2 and lies on line 1 (i.e., the intersection of line 1 and line 2); and $x_3$ is the source of line 3 and lies on line 2 (i.e., the intersection of line 2 and line 3).
The two distributions, $\mathcal{R}\_\mathcal{L}^\alpha f_\mu$ and $\mathcal{R}\_\mathcal{L}^\alpha f_\nu$, are supported on the 9 points in the tree. Their values at the projection points $a_i$ and $b_i$ are defined as described above, while their values at the nodes $x_i$ are $0$. In this case, the tree contains 8 edges, which are:
$e_1=(x_1,a_1),e_2=(a_1,b_1),e_3=(b_1,x_2),e_4= (x_2,a_2),e_5=(a_2,b_2),e_6=(b_2,x_3),e_7=(x_3,b_3),e_8 = (b_3,a_3).$
In Equation (13), the weight $w_e$ is defined as the Euclidean distance between the endpoints of edge $e$. The term subtree is used in its standard graph-theoretical sense. Below Figure R3, we provide the explicit computation of the terms $\mathcal{R}\_\mathcal{L}^\alpha f_\mu(\Gamma(e_i))$.
Note that, *the choice of the root in the tree does not affect the final result*, since it is the Wasserstein distance between $\mathcal{R}\_\mathcal{L}^\alpha f_\mu$ and $\mathcal{R}\_\mathcal{L}^\alpha f_\nu$—two distributions defined over the tree system $\mathcal{L}$. The availability of this closed-form expression is a valuable feature, as it enhances computational efficiency and represents a non-trivial generalization of the closed-form solution for the one-dimensional Optimal Transport problem.
We believe the explanation provides a clearer understanding of Eq.(13).
**Sorting operation.** Sorting operations are used to determine the edges of the tree. For example, in the case above, sorting is applied separately to the set of points on each line. On line 2, after sorting the four points, we obtain the order $x_2 \rightarrow a_2 \rightarrow b_2 \rightarrow x_3$, which defines three edges: $e_4 = (x_2, a_2)$, $e_5 = (a_2, b_2)$, and $e_6 = (b_2, x_3)$.
Note that, if $x$ and $y$ were positioned differently in space, their projections onto line $i$ could lie outside the segment between $x_i$ and $x_{i+1}$. This highlights one of the key differences between the Optimal Transport problem on the real line $\mathbb{R}$ and on tree metric spaces. **Figure R4** presents the outcome when $x$ and $y$ are placed differently in space compared to Figure R1. The projection and mass computation steps remain unchanged (though $\alpha(y)$ may differ due to new location of $y$). However, the resulting tree structure changes—for example, the subtree $\Gamma(e_3)$ now contains only the point $b_1$, while $\Gamma(e_5)$ includes $b_2$, $x_3$, $b_3$, and $a_3$.
---
We sincerely thank the reviewer for their valuable and constructive feedback. Given that the rebuttal process permits only a single response, we have made every effort to clarify all potentially remaining questions in this reply. If the reviewer finds our clarifications satisfactory, we kindly ask that you consider raising the score.
---
*Update.* Thank you for your response. We will include the additional explanation in the revision. | null | null | null | null | null | null |
When Bad Data Leads to Good Models | Accept (poster) | Summary: The paper makes the claim that bad data is important to include during LLM pretraining. The authors include a variety of experimental results in support of this claim to show that by including a greater percentage of toxic data during pretraining, downstream alignment can be further improved.
Claims And Evidence: I do not find the claims and evidence to be convincing. I do understand the authors' intuition that including more toxic data during pretraining might lead to more separable representations, which could help make alignment methods more effective; in fact, I was hopeful while reading the paper that there would be strong evidence in support of this. However, the experimental methodology is not convincing. In particular, the experiments are conducted on small-scale 1B models, although it has been significantly discussed in prior work that post-training generalization can vary dramatically with model size. As such, it is difficult to draw strong conclusions about pre-training best practices from these results alone.
The main finding in support of the author's central claim appears to be based on the inference time intervention results (the authors find that with more toxicity, ITI can achieve less toxicity). While these results are positive, I am concerned about the novelty of this finding, and the lack of additional experiments to support the central claim. Prior work in representation learning [1] has already discussed the notion that by including a greater proportion of a second data distribution during training, representations for the respective distributions become more separable. It naturally follows that they would be easier to steer at inference time; this does make for an interesting experiment, but should be supplemented with further experiments.
Additionally, the authors appear to use off-the-shelf post-trained models for their DPO/SFT comparisons in Table 1, but state that the results on these models demonstrate better alignability as a result of including toxic data during pretraining. Can the authors clarify exactly how these experiments were performed?
[1] Jianwen Xie, Ruiqi Gao, Erik Nijkamp, Song-Chun Zhu, Ying Nian Wu. Representation Learning: A Statistical Perspective (2019).
Methods And Evaluation Criteria: Something I found concerning was that in the 3rd paragraph of Section 5.3, the authors write "we observe that our method, with weak
intervention strength, outperforms all baselines in detoxification while maintaining the lowest cross-entropy loss." However, the method of ITI was introduced in prior work and not by the authors, so the authors have not introduced a method in this work. Therefore, the framing that a method was introduced in this paper (which I am interpreting by the use of the word "our") that outperforms prior work is confusing/actively misleading. Nonetheless, the ITI experiment does make sense and does partially support the authors' central claim. However, as mentioned in my other comments, I think that more experimentation should have been done on measuring the effectiveness of post-training methods (like SFT and DPO), as the fraction of toxicity during pre-training is varied.
Theoretical Claims: There are no theoretical claims made.
Experimental Designs Or Analyses: Additionally, I found the "Motivating Experiment" Section in Section 2 to be confusing and out-of-place for the paper. The authors discuss superposition at length, as well as a toy experiment on how entanglement is affected by data composition, but it is not clear how these results are relevant for the rest of the paper, and in particular the broader claim about how "bad data leads to good models." I think the space taken by this section would have been better utilized with further experiments on measuring alignment methods' performance after including toxicity in pre-training.
As far as the included experiments are concerned, the authors seem to only focus on the ITI method, which limits the conclusions that can be drawn from the results. Namely, I can only confidently conclude that by including toxic data during pretraining, toxic representations become more separable from benign data, which leads to better steerability. However, this is a natural conclusion from prior work, and would unfortunately not constitute a sole conference paper at ICML.
Supplementary Material: I did look at the supplementary material.
Relation To Broader Scientific Literature: The paper fits into the broader literature of LLM pre/post-training, as well as adversarial robustness and alignment methods.
Essential References Not Discussed: The authors do not appear to cite a significant body of prior work on representation learning, which some of their discussion would benefit from.
Other Strengths And Weaknesses: I think the authors are investigating a genuinely interesting problem, and as mentioned earlier, I was hopeful for the results to be in strong support of their claim. I think the intuition behind including toxic data distributions during pre-training makes sense. However, to meet the bar for ICML, such intuitions should be supported by substantial empirical evidence with good presentation. I discuss most of my concerns with experiments in the "Claims and Evidence" section above.
Other Comments Or Suggestions: I think the presentation at large needs to be cleaned up. As mentioned, the discussion on superposition in Section 2 feels less relevant to the rest of the paper. Also, I found the formatting of Table 1 difficult to read at a glance. It's still not obvious to me whether DPO/SFT models in Table 1 were post-trained by the authors or used off-the-shelf from prior work.
Questions For Authors: Were the DPO/SFT models used in Table 1 off-the-shelf models, or did you post-train these models yourselves?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank the reviewers for their thoughtful feedback and insightful questions; please see our point-by-point responses below. Thanks for pointing out the typo and improved plotting, we've updated our draft.
## Difficult to draw strong conclusions from experiment on 1B level model
We acknowledge that our experiments are conducted at the 1B scale, which may limit the generalizability of conclusions. However, our goal is not to make definitive claims about scaling laws, but to provide a clean and controlled case study on how toxic data influences representational structure and post-training alignability. We believe this foundational insight motivates broader scaling studies in future work.
## Result is trivial considering prior work [1]
Thanks for pointing out the insightful paper. We will include a detailed discussion in the revision. However, instead of saying our findings are trivial, we'd argue that they provide solid experimental support for the theoretical analysis in [1]---introducing the training data of a second feature can improve this feature’s separability. In a way, we are applying the idea in [1] to LM pretraining, a downstream application and there are interesting findings along the way.
There are two points of distinction:
(1) The connection between separability and steerability is non-trivial. Prior work, such as on superposition, suggests that when the representation space is compact, neural networks may superimpose new features on top of existing ones—making steering more difficult even a feature is well-learned/separated.
(2) Moreover, we demonstrate that the relationship between pretraining frequency and post-training steerability is **not linear**: there exists an optimal level of toxic data that maximizes steerability, and this level is significantly lower than for non-toxic data. This non-trivial insight is further supported by experiments with SFT and DPO.
## "Motivating Experiment" Section is out of place
The motivating experiment presents a simple toy case when increasing the frequency of a certain underrepresented feature could improve its entanglement with other features in a crowded space. We will consider moving it to appendix if the space doesn't allow with newly added experiments.
## Concerns around phrasing ITI as “ours”
"Our method" refers specifically to “pretraining with toxic data,” not ITI. We have edited the language throughout to clarify this. Thanks for the suggestion!
## Additional experiments on SFT/DPO
We agree it is important to examine how performance scales with increasing levels of toxic pretraining data. As suggested, we conducted further experiments using SFT and DPO on models trained with 0%, 5%, 10%, 15%, and 20% 4chan data. The dataset used is listed in the section in L328.
These results will be added to **Table 1** and **Figure 6**:
**Table 1’**: Effectiveness of SFT at different pretraining toxic data levels.
| Toxic % | Toxigen ↓ | RTP ↓ | CE Loss ↓ |
|---------|-----------|--------|------------|
| 0% | 39.27 | 28.00 | 2.68 |
| 5% | 38.40 | 26.21 | 2.69 |
| 10% | 37.62 | 25.78 | 2.71 |
| 15% | 37.45 | 25.81 | 2.73 |
| 20% | 38.20 | 26.39 | 2.75 |
**Table 2’**: Effectiveness of DPO at different pretraining toxic data levels.
| Toxic % | Toxigen ↓ | RTP ↓ | CE Loss ↓ |
|---------|-----------|--------|------------|
| 0% | 38.86 | 29.67 | 2.71 |
| 5% | 33.91 | 19.85 | 2.70 |
| 10% | 27.45 | 13.02 | 2.73 |
| 15% | 26.88 | 13.19 | 2.74 |
| 20% | 29.34 | 15.97 | 2.75 |
We observe a **smile-shaped curve** in both SFT and DPO performance. Our method—adding toxicity during pretraining—also enhances the detoxification effectiveness of these post-training techniques, suggesting our findings apply beyond linear steering to holistic fine-tuning methods. | Summary: This paper examines whether training on more toxic data in LLMs can reduce toxicity by enabling more disentangled features (which recognize toxicity) and then reducing the contribution of those features. They show in a toy setting how training on more data helps disentangle features. Afterwards, the authors then conduct pretraining experiments with OLMO and show that adding more toxic data + ITI helps reduce toxicity more than baseline toxicity reduction methods.
Claims And Evidence: See strengths and weaknesses
Methods And Evaluation Criteria: See strengths and weaknesses
Theoretical Claims: See strengths and weaknesses
Experimental Designs Or Analyses: See strengths and weaknesses
Supplementary Material: See strengths and weaknesses
Relation To Broader Scientific Literature: See strengths and weaknesses
Essential References Not Discussed: See strengths and weaknesses
Other Strengths And Weaknesses: # Strengths
- The authors study how pretraining data mixtures affect the entanglement of LLM features. This is a large-scale experiment, so results will likely transfer to frontier models.
- The results show that toxicity can be mitigated with appropriate ITI.
# Weaknesses
- These results have been somewhat observed in prior papers, as mentioned by the authors. As a result, this result may be less exciting for most practitioners.
- There's no scaling experiment investigating the ratio of toxic data required for larger models. Do we need more or less toxic data? I'd imagine it would be less data but it would be useful to include this experiment (although I realize it's expensive) as I believe it would strengthen the argument of the paper.
- There's no investigation of any of the limitations of training on more toxic data. Is it possible that it becomes easier to jailbreak the model into saying toxic text? How much does training on more toxic data increase pretraining cost? Does the model's performance on MT-bench drop?
- One of ITI's weaknesses is that the activation direction chosen might not be robust to finetuning, so any finetuning would require further calibration and make the method more unwieldy.
Other Comments Or Suggestions: Typos:
- L253: and toxicity detection using ToxiGen We --> and toxicity detection using ToxiGen. We
- Figure 5: can you add the mean of the distribution as a dashed line for skimmability?
Questions For Authors: I'm happy to raise my score to a 3 if most of the following experiments are conducted:
1. Would it be possible to scale the model size and see what the optimal amount of toxic data for ITI is? Does it increase or decrease with model size?
2. Can you attempt to jailbreak the ITI model using GCG or some prompting baseline? Is this easier to accomplish on models trained with more toxic data during pretraining?
3. Can you eval the models on MT-bench along with MMLU?
4. Can you finetune on additional data and see if the intervention direction found with ITI is robust? Do you need to recalibrate the method?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewers for their thoughtful feedback and insightful questions; please see our point-by-point responses below. Thanks for pointing out the typo and improved plotting, we've updated our draft.
## **Concern**: These results have been somewhat observed in prior papers, as mentioned by the authors. As a result, this result may be less exciting for most practitioners.
If you are referring to Longpre et al. (2023), we agree that similar observations have been made regarding the tradeoff practitioners face when deciding how much toxic data to retain during pretraining. The key difference here is Longpre et al only evaluated the pretrained models' performance, but we extend the investigation to treating pretraining and post-training not as isolated steps, but as a **unified system**.
Rather than focusing solely on the pretrained model’s behavior which is discussed in Longpre et al. (2023), we investigate how the **customized behavior after post-training methods**—such as prompting and activation steering—depends on the nature of pretraining data. In this context, we hypothesize (and our experiments support) that **increasing the proportion of toxic data during pretraining can improve the alignability** of downstream behavior—**up to an optimal threshold**. This insight offers practitioners a new perspective: toxic data, when used judiciously, may enhance rather than hinder post-training effectiveness.
## Scaling Model Size and Optimal Toxic Data
Though this is a great suggestion and would help truly convince practitioners to modify their data composition, we believe it represents a broader research problem than what can be fully addressed within the scope of this paper. The optimal amount of toxic data likely depends not only on model size, but also on the specific types of clean and toxic data used, as well as the particular post-training technique applied. Ultimately, we view this as an empirical question and plan to explore it further in future work on data mixture scaling in pretraining.
## Jailbreaking via GCG or Prompting
We have not tested GCG directly, but we evaluated the model using Real Toxicity Prompts—a set of **jailbreaking** queries likely to elicit toxic completions. Table 1 shows that ITI + toxic-trained models produce less toxic continuations, suggesting prompt-based jailbreaking is harder when more toxic data is used in pretraining with ITI applied.
## MT-Bench Evaluation
MT-Bench is designed for instruction-tuned, multi-turn conversational models. Our model is a text generator without instruction tuning, so we do not consider MT-Bench an appropriate benchmark. To assess capability impact from toxic data, we provide results on 9 additional datasets in Appendix A.
## ITI Robustness After Finetuning
A model’s representation space can change after finetuning, so alignment techniques like ITI would generally need recalibration. This is a general issue in model safety, not unique to our approach [1,2]. The good thing here is that the ITI training process is so light that it can be redone easily.
[1] Fine-tuning aligned language models compromises safety, even when users do not intend to!
[2] Emergent Misalignment: Narrow finetuning can produce broadly misaligned LLMs
---
Rebuttal Comment 1.1:
Comment: > The key difference here is Longpre et al only evaluated the pretrained models' performance, but we extend the investigation to treating pretraining and post-training not as isolated steps, but as a unified system.
Ah I see that your intro has that framing; I think after reading the abstract I didn't catch the entire framing. Maybe consider reframing the first two lines of the abstract from "In large language model (LLM) pretraining, data quality is believed to determine model quality. In this paper, we challenge the notion of “quality” in the context of post-training" to something like "In large language model (LLM) pretraining, data quality is believed to determine model quality. In this paper, we re-examine quality from the perspective of the entire pre-training + post-training pipeline."
(Although what I wrote is poorly written, I think an image describing the entire system (rather than 'in the context of finetuning') might be a better picture to evoke.
> We have not tested GCG directly, but we evaluated the model using Real Toxicity Prompts—a set of jailbreaking queries likely to elicit toxic completions. Table 1 shows that ITI + toxic-trained models produce less toxic continuations, suggesting prompt-based jailbreaking is harder when more toxic data is used in pretraining with ITI applied.
I don't think Real Toxicity Prompts are realistic examples of jailbreaks. The GCG experiment doesn't seem that hard to run, but upon reflection it's a bit of a circuitous way to answer the question 'Are models with more linearly separable features more easily induced to elicit those features (e.g., via jailbreaking)'.
> Our model is a text generator without instruction tuning, so we do not consider MT-Bench an appropriate benchmark.
Sorry; I did not realize there were additional results in the Appendix. However, I looked at the Appendix A and these results aren't as surprising, because there was the same amount of C4 data used.
I feel like this is an unfair comparison because the models with more % toxicity data are trained with more tokens, whereas in reality one would want to only train with a fixed amount of tokens (so as not to violate Chinchilla scaling laws) for a fixed model size (although I guess in practice there's too few tokens for most models). If you have checkpoints for the 5 models with nonzero toxicity data that were early-stopped (so as to be trained with the same number of FLOPs as the zero toxicity data model), would it be possible to include these MMLU numbers?
----------
I feel like this paper is a 2.5 because the experiments are a bit thin, but I do like the results. I'm happy to raise my score to a 3 if the more fair comparison of checkpoints is run + GCG (even though I don't think it's that informative, it would still be a novel and interesting result).
---
Reply to Comment 1.1.1:
Comment: Thanks for the suggestions on framing abstract, we've edited accordingly.
Below are the GCG results on the model trained with 0% or 10% toxic data, with or without strong ITI intervention. We ran GCG on 200 prompts sampled from the AdvBench dataset (the evaluation dataset used in the GCG paper) and reported the attack success rate.
| ITI Strength (% Toxic Pretraining) | None (0%) | None (10%) | Strong (0%) | Strong (10%) |
|----------------------|-----------|------------|-------------|--------------|
| Attack Success Rate | 80% | 82% | 46% | 38.5% |
We find that the model with more toxic pretraining is harder to jailbreak using GCG when ITI is applied, compared to the model trained without toxic data. When ITI is not applied, both models are vulnerable to GCG jailbreaks, with the toxic-trained model being slightly more susceptible. We will include a discussion of this result in the revision.
We also checked out the checkpoints with the same number of training tokens but different proportions of toxic data. Here is a summary of their MMLU accuracies. The minimal change in scores are similar to toxic data proportion is similar to what we saw in Figure 4.
| Toxic Data Proportion | 0% | 5% | 10% | 15% | 20% | 25% |
|-----------------------|------|------|------|------|------|------|
| MMLU Accuracy (%) | 31.2 | 31.5 | 32.1 | 32.4 | 32.8 | 31.4 | | Summary: The paper challenges the conventional belief that filtering out toxic data from the pretraining corpus of large language models (LLMs) is always beneficial. The authors argue that including toxic data in pretraining can improve the model's ability to control and reduce toxicity during post-training, ultimately leading to better-aligned models.
Claims And Evidence: The paper presents solid experimental results and evaluations to support their claims.
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: This work challenges the conventional belief that filtering toxic data from the pretraining corpus of LLMs is always beneficial. It finds that toxic data in the pretraining corpus actually help the model learn a better representation of "being toxic." As a result, the model achieves improved detoxification performance at inference time when using the intervention method such as ITI.
Essential References Not Discussed: Essential references are discussed.
Other Strengths And Weaknesses: The study focuses primarily on toxicity and does not explore whether the findings generalize to other types of "bad data" (e.g., biased, harmful, or hallucinations).
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the encouraging comments! | Summary: This paper proposes a novel approach to improving the performance of LLMs by incorporating toxic data during pretraining. The authors suggest that including a controlled amount of toxic data in pretraining, when combined with post-training techniques, can lead to better overall performance. To investigate this, they conduct extensive experiments on the Olmo-1B model, varying the proportion of toxic data in the pretraining corpus up to 25% of the total tokens. Their results show that models pretrained with more toxic data achieve higher accuracy on both the MMLU benchmark and toxicity detection tasks and lead to less toxic generation. The key intuition behind this finding is that if a base model learns toxic concepts more effectively during pretraining, it becomes easier to mitigate toxicity through post-training interventions. Additionally, the paper provides a theoretical justification for this phenomenon by introducing the concept of feature entanglement.
## update after rebuttal
Thank author for sharing new insights. No change are made. I am looking forward to "Role of Model Size in Optimal Toxic Data %" study in future work.
Claims And Evidence: Claim in this paper is well supported by theoretical argument on feature entanglement. The model training result on Olmo-1B also supports author's claim.
Methods And Evaluation Criteria: - Author used MMLU, Toxigen, C4, and 4chan dataset. Those are commonly used data for LLM toxicity tasks. Those dataset well supports authors' claim and experiment
Theoretical Claims: Author introduced theoretical proof on Entanglement of features. I manually verified this entanglement lower bound proof through frame theory. I also manually verified 2D and 3D space cases.
Experimental Designs Or Analyses: Experiment shows key evidence support the claim.
1. Experiment shows increasing proportion of toxic training data result in more toxic generation if no intervention applied.
2. When apply Inference-time Intervention, model trained using more toxic data result in lower toxicity aligned with authors' claim and theoretical analysis.
3. Experiment also shows with increasing toxicity data, model shows better MMLU performance and toxicity detection performance. With toxicity detection performance significantly improved at 25% toxicity data.
4. Author also compared multiple post training methods including Prompting, MEDA and INST, SFT, and DPO.
Critiques
1. The main concern is in Fig. 6, the decreasing trend on toxicity VS. toxic training data is not monotonic. Model performed the best at 10% with strong steering. Author doesn't explain why 10% shows the optimal performance, and there is no hypothesis on this.
2. Pretrain used clean + % of toxic data up to 25%. While increasing toxic data, clean data kept constant, therefore, the total amount of training token changed, would this impact model MMLU result in Fig. 4? Increasing training data size may reduce model's toxicity in general.
Supplementary Material: Yes, I reviewed all Supplementary materials.
Relation To Broader Scientific Literature: Model alignment and safety has been widely studied in the past. Reducing generation toxicity while maintaining model's generation quality has always been a difficult task with wide industrial application. This paper leveraged feature entanglement framework build by Elhage
et al. (2022), and give clear theoretical justification on why including bad data is important to train a good model. This work has application in industry as well, proposing a novel approach on how to reduce model generation toxicity.
Essential References Not Discussed: Not that I am aware of.
Other Strengths And Weaknesses: - Provide sound theoretical justification and toy experiment to support feature entanglement argument.
- Experiment are quite comprehensive comparing
Other Comments Or Suggestions: N/A
Questions For Authors: 1. Why do you use Olmo-1B model on this task instead of 7B based model such as Llama?
2. Would the model size be an important factor in determining the optimal percentage of toxic data?
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We thank the reviewers for their thoughtful feedback and insightful questions; please see our point-by-point responses below.
## Non-Monotonic Toxicity Trend in Fig. 6
We will add a discussion in L318 (right column) to address this:
The initial decrease in toxicity is due to the model learning a more separable toxic representation, as toxicity is underrepresented in the original dataset. This disentanglement enables better detoxification via ITI and prompting. The later increase stems from overrepresentation of toxic features, which become entangled with underrepresented clean features again.
## Impact of Varying Token Counts on MMLU
Figure 4 shows MMLU performance remains stable despite increased toxic data, suggesting the relevant knowledge is primarily derived from the clean data.
## Role of Model Size in Optimal Toxic Data %
This is a valuable point. We believe the optimal toxic data amount depends on both model size and the nature of the data. A comprehensive study is needed to understand how data mixture scaling impacts performance, and we defer this to future work. | null | null | null | null | null | null |
A Physics-Informed Machine Learning Framework for Safe and Optimal Control of Autonomous Systems | Accept (poster) | Summary: This work develops a physics-informed learning approach for constrained optimal control problem, where the performance objectives are represented using a cost function and safety conditions are formulated using state constraints. A conformal prediction-based safety verification approach is developed with probabilistic error bound on performance degradation. Three simulation examples are provided to demonstrate the performance of the approach.
Claims And Evidence: The contribution is clear and mostly supported by the mathematical exposition and simulation results. The paper makes an interesting contribution relevant to the machine learning, controls, and robotics communities. However, claiming that the paper develops a novel physics-informed machine learning framework is misleading because the paper does not provide any fundamentally new physics-informed machine learning method; the development is mostly a direct application of well-known physics-informed machine learning methods.
Methods And Evaluation Criteria: The methodology and evaluation criteria is appropriate.
Theoretical Claims: 1. The theoretical claims (Theorems 1 and 2) appear correct.
2. However, it is not clear if the cost function and safety constraints need to be convex. Are the authors claiming the method applies to non-convex optimal control problems? Some theoretical exposition in this regard would improve the quality of the paper.
3. The training loss in (8) and (9) do not appear to have a regularizing term (e.g., Tikhonov regularization). In physics-inforrmed learning, having a regularizing term in the loss is important as it can prevent the value function estimate from learning a trivial solutions that would yield a zero PDE residual error and also mitigate overfitting. Furthermore, the authors could also include penalty terms to penalize undesirable values of \hat{V}_{theta}, use it as a constraint in the training, or encode hard constraints in the NN architecture itself (see Lyapunov-Net reference below).
4. The paper claims the auxiliary value function is a unique continuous viscosity solution to the HJB, citing the reference (Altarovici et al., 2013). However, (Altarovici et al., 2013) makes this claim under multiple assumption (see A1-A4 in that result), one of which is that the dynamics f(x,u) be globally Lipschitz in x which highly restrictive for most practical applications). The paper makes no mention of these assumptions. Furthermore, the viscosity solutions are only guaranteed to be continuous and there are no guarantees on its differentiability. However, the control policy is dependent on the derivative of the auxiliary value function. Without differentiability, the feedback law might not be well-defined.
5. The approach using safety verification with conformal prediction is interesting.
References:
Gaby, N., Zhang, F. and Ye, X., 2022, December. Lyapunov-net: A deep neural network architecture for lyapunov function approximation. In 2022 IEEE 61st Conference on Decision and Control (CDC) (pp. 2091-2096). IEEE.
Altarovici, A., Bokanowski, O. and Zidani, H., 2013. A general Hamilton-Jacobi framework for non-linear state-constrained control problems. ESAIM: Control, Optimisation and Calculus of Variations, 19(2), pp.337-357.
Experimental Designs Or Analyses: 1. The experimental methodology is mostly appropriate. The results are shown to be applicable for high-dimensional systems (20 dimensional system in the multi-agent navigation case).
2. The paper assumes known dynamics which by itself is not problematic, but what would happen if the dynamics have modeling uncertainties and/or disturbances? In practice, this is usually the case, so the experiments need to account for such modeling uncertainties to be realistic.
3. One of the benefits of using physics-informed neural networks is that one can obtain good performance with fewer training samples. The experiments use 65,000 training points. What would happen if fewer datapoints are used.
Supplementary Material: I reviewed the Appendix.
Relation To Broader Scientific Literature: The key contributions are related to approximate dynamic programming (ADP) and physics-informed machine learning research. Notably, value function approximation using neural networks is not new, the authors can discuss more relevant ADP papers/optimal control papers to put contribution in context. The authors can also discuss more physics-informed machine learning literature.
Essential References Not Discussed: The following reference is relevant and needs to be discussed in the introduction:
Fotiadis, F. and Vamvoudakis, K.G., 2023, December. A Physics-Informed Neural Networks Framework to Solve the Infinite-Horizon Optimal Control Problem. In 2023 62nd IEEE Conference on Decision and Control (CDC) (pp. 6014-6019). IEEE.
Other Strengths And Weaknesses: None
Other Comments Or Suggestions: None
Questions For Authors: None, please see the previous comments
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Method application to non-convex OCP
Our method extends beyond convex OCPs. While a convex cost function leads to a convex epigraph formulation that standard optimizers can efficiently solve, our approach is not restricted to them. By leveraging dynamic programming to solve the epigraph formulation, we obtain a general HJB-VI, which is well-suited for handling both convex and non-convex settings. In fact, our experiments explicitly demonstrate this capability by incorporating non-convex and even disconnected safety constraint sets.
# Tackling Model Uncertainty/Disturbances
This study pioneers a learning-based approach to jointly optimize safety and performance using HJ Reachability, assuming accurate model information. Extending it to account for model uncertainty is a key future direction. As an initial step, we can follow [3] to handle dynamics uncertainty, modelling it as $\dot{x}(t) = f(x(t), u(t), d(t))$, where $d(t)$ captures learning uncertainty, unmodeled dynamics, or disturbances. We then define a robust auxiliary value function $\hat{V}$:
\begin{equation}
\hat{V}(t, x(t), z) = \min_{\textbf{u}} \max_{\textbf{d}} \max \{C(t, x(t), \textbf{u}, \textbf{d}) -z, \max_{s \in [t, T]}g(x(s)) \}.
\end{equation}
The auxiliary value function optimizes performance cost under worst-case uncertainty while guaranteeing safety. As with the non-robust formulation, it is characterized as the unique viscosity solution of the HJI-VI:
\begin{equation}
\min\Bigl(-\partial_t \hat{V} - \min_{u} \max_{d} \langle \nabla_{\hat{x}}\hat{V}(t, \hat{x}), \hat{f}(\hat{x}, u, d)\rangle ,\hat{V} - g(x)\Bigr) = 0,
\end{equation}
To incorporate uncertainty (e.g., model errors or adversarial settings), we solve the PDE using our proposed method. As an initial validation, we apply it to the Pursuer-Evader problem with uncertainty in the evader model, capturing potential variability in human behavior. Figure 1 (https://shorturl.at/sxkvw) illustrates this: dashed lines show undisturbed trajectories, while solid lines depict uncertain cases where the evader moves unpredictably. The pursuer adapts with sharper turns, ensuring robust tracking despite uncertainty. Future work will further explore uncertainty handling.
# Training loss does not have a regularizing term
To mitigate trivial solutions, we employ the adaptive loss balancing strategy from [5], which dynamically adjusts $\lambda$ at each training step to balance the boundary loss and PDE loss. This ensures both objectives are enforced jointly.
As future work, we plan to incorporate explicit regularization, such as Tikhonov ($L_2$) regularization, to prevent overfitting and improve generalization. Additionally, we will explore hard constraint enforcement techniques within the neural network architecture—such as those proposed in [1,2]—to exactly satisfy boundary conditions and enhance the fidelity of the learned value function.
# Missing Assumptions
We appreciate the reviewer for highlighting the missing assumptions. In the revised manuscript, we will explicitly state those assumptions. In practice, assuming local Lipschitz continuity is often sufficient, particularly when the value function needs to be computed over a compact state space, as is often the case with PINN training (including our work). Under this assumption, the continuity and the well-posedness of the HJB solution can still be ensured without requiring global Lipschitz continuity. We will revise the manuscript accordingly to clarify the assumptions and better contextualize their relevance in practical settings.
# Differentiability of $\hat{V}$
We approximate the value function using a PINN with *sinusoidal* activations, ensuring smoothness and differentiability of the value function. Thus, the feedback control law, derived from the value function gradients, is well-defined and implementable.
# Fewer Training Samples to train PINNs
Since our approach is entirely self-supervised, generating training data is computationally inexpensive. Thus, we use a large number of training points (65K) to promote stability and convergence during training. However, we acknowledge that fewer points may be beneficial in high-dimensional cases to reduce memory and computation. While not explored here, we will investigate trade-offs between sample efficiency and performance in future work.
# Essential References Not Discussed
We thank the reviewer for the suggestion. We will include [4] as well as an analysis of other PIML approaches for HJ Reachability and optimal control in the revised manuscript.
# References
[1] Gaby et al. (2022). Lyapunov-net for Lyapunov function approximation. IEEE CDC.
[2] Singh et al. (2025). Safety boundary conditions in neural reachable tubes. IEEE ICRA.
[3] Bansal et al. (2017). Hamilton-Jacobi reachability. IEEE CDC.
[4] Fotiadis & Vamvoudakis (2023). PINNs for infinite-horizon control. IEEE CDC.
[5] Wang et al. (2021). Gradient flow pathologies in PINNs. SIAM J. Sci. Comput. | Summary: In this work, the Authors propose a novel framework for the certified safety of autonomous agents based on the combination of the epigraph-based formulation of the optimal control problem, DeepReach, and conformal predictions. They test the proposed framework in three simulated environments and show the advantage of the proposed framework over the models that either mostly focus on performance or mostly focus on safety.
Claims And Evidence: The work follows the standard routine in the field of the safety of autonomous agents. As a result, the claims here are supported by the standard means, previously validated in the related research.
Methods And Evaluation Criteria: I found this work to present a step in the right direction. Naturally, the next step after having DeepReach, a neural network model for solving the Hamilton-Jacobi Reachability problem, was to extend it with the safety guarantees accounting for the errors potentially made by the deep learning model. I have, however, the following concern regarding the type of the guarantees provided by the conformal predictions, as follows. Equation 15 formulates the probability of the safety violation per state $\hat{x}$ in $S_\delta$. It would seem that, for longer trajectories, this quantity would accumulate, making the target values of $\epsilon$ low. How low exactly and how strong the safety requirements would be in that case is a question that, I believe, is important to investigate and answer. At the same time, I would like to notice that this form of guarantee is a huge step forward compared to the cumulative guarantees used previously with conformal predictions, as they did not preclude the possibility of short-term safety violations.
Additionally, I would like to note that the very same machinery applied here to the cost estimate in Theorem 2 makes perfect sense to me. As point violations of this estimate are not safety-critical, conformal predictions here offer a nice way to make that estimation that, on average, should be correct.
Theoretical Claims: I have checked the theoretical claims. While the theory looks mostly correct and follows the standard practices in the field, my biggest question is related to the i.i.d. assumption in both Theorems 1 and 2. While I understand that this assumption is central for using the conformal predictions (e.g. through Lemma 1 of Supplementary Material), I am not sure if its use is justified here for the following reason. While under this assumption $N_s$ is sampled i.i.d. from $S_\delta$, this is arguable not where the states of interest reside. The states of interest, balancing safety and performance, seem likely to reside on the edge of the set $S_\delta$ ($=\partial S_\delta$); thus the i.i.d estimation may be biased.
If I am correct, two ways to mitigate that potential issue are:
- to set $\alpha=1$. If it wouldn’t affect the value of $\beta$ as a function of $\epsilon$ terribly, that would allow circumnavigating the entire machinery of the conformal predictions, instead converging to a trivial limit-case result from combinatorics (which was also a nice way for me to check that the equations are correct)!
- to perform an empirical study where the numbers of safety violations would be measured as a function of $\alpha$ and $\beta$ to see if the simulated experiment reproduces the theoretically predicted trend.
I suggest trying both options as they are easy to try and have the potential of making the results here stronger.
Another question that I have is: the framework seems to assume that the deviations of the neural network model solutions from the actual solutions are local and do not accumulate over time. It would be nice to hear the argument regarding why this might be the case.
Experimental Designs Or Analyses: The testing scenarios and baselines here appeared overly simple to me. While there’s nothing wrong with this, typically the related research in the field has used stronger benchmarks, both simulated and data-driven, and considered stronger baselines. There have been lots of advancements in the field lately; it would be nice to compare some of those – per Authors’ choice – to the proposed model.
Supplementary Material: I have read the proofs and model descriptions in the supplementary material, then glanced through everything else.
Relation To Broader Scientific Literature: The work is rooted in the host of prior literature. Specifically, the Hamilton-Jacobi Reachability, the epigraph formulation of the optimal control problem, DeepReach, and conformal predictions are at this point all well-established tools used in the certified safety of autonomous systems. The combination of DeepReach and the conformal predictions that is aimed to reinstate the certifiable safety in the model that otherwise computed a solution through a deep neural network, is a novel and natural step forward for that line of research.
Essential References Not Discussed: I feel like some further, newer references could be added to the Introduction to better reflect the current state of the research in the field. Perhaps, review papers such as the one on The Safety Filter by Jaime Fisac’s group could be a good addition here.
Other Strengths And Weaknesses: Strength: the text is mostly clearly written. Combined with a well-structured research project, it is a pleasure to read.
Weakness: the methods are not fully documented. It is important to detail, in the Methods section, the details of the training (beyond the structure of the neural network that is present in Appendix).
Other Comments Or Suggestions: N/A
Questions For Authors: - Why is the i.i.d. assumption made in both theorems?
- Why is the assumption of stability (i.e. that $\delta$ does not grow over time) made in the model?
- What would be the relevant values of $\epsilon$ and $\beta$ provided that the quantity in Equation 5 would accumulate over time and states traversed?
- What was the training procedure for the curriculum learning?
- Could you perform an experiment to show that the theoretically derived relation between $\alpha$, $\beta$, and $\epsilon$ holds?
I am happy to update my score based on the answers to these questions.
__________________________________
Post-rebuttal: my questions and concerns were mostly addressed; raising the score.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Clarification on Curriculum Learning
As discussed in Sec. 3.1, we first pre-train the DNN to learn the value function at the terminal time ($t=T$)—i.e., the boundary condition of the HJB-VI—using $\lambda = 0$. We then apply curriculum learning, gradually decreasing $t$ from $T$ to $0$, so the terminal value function propagates backward per the HJB-VI. At each iteration, we uniformly sample $N$ states and time points from [$t, T$]) and train using the loss in Eq. (10).
# Clarification on Verification Procedure
We would like to provide further clarification on the proposed verification procedure. First, we estimate the induced policy $\hat{\pi_{\theta}}$ from the learned value function $\hat{V_{\theta}}$. Next, we generate 300K rollouts from $t = 0$ to $t = T$, starting from various initial states $\hat{x_0}$, and compute the corresponding rollout costs $\hat{V}_{\hat{\pi}}$. We then apply conformal prediction to compute the correction $\delta$, which represents the safety correction over the **entire trajectory** from $t = 0$ to $t = T$. Thus, the violation probability $\epsilon_s$ is defined for the full trajectories starting from $\hat{x_0}$, not individual states.
# Why $\delta$ Does Not Grow Over Time
As discussed above, the correction term $\delta$ is based on the rollout cost evaluated over the entire trajectory from $t = 0$ to $t = T$. If, instead, the cost were evaluated starting later in the trajectory, i.e., from $t = t_0$ to $t = T$ for some $t_0 > 0$-the trajectory would typically experience fewer safety violations, since early violations are excluded from the cost computation. Thus, the magnitude of $\delta$ at the beginning of the trajectory is greater than or equal to its magnitude at any later time. This property ensures that the initial correction term is conservative enough to account for worst-case safety costs, leading to robust safety guarantees.
# i.i.d. Assumption in Theorems
We assume i.i.d. sampling over the safe set as we lack prior knowledge of the test-time initial state distribution. This ensures generality in our safety guarantees. If a specific initial state distribution is of interest, it can be used for sampling instead to obtain tighter safety estimates. To reduce reliance on distributional assumptions, one can also adopt a worst-case approach by setting $\alpha = 0$, as the reviewer suggested.
# Potential bias from sampling near $\partial S_{\delta}$
While states delicately balancing safety and performance often reside near $\partial S_{\delta}$, learning errors can occur anywhere in $S_{\delta}$. Sampling only near the boundary may underestimate violations in the interior, which can be problematic if the initial states of interest during the test time are inside $S_{\delta}$. In the absence of prior distribution knowledge, we adopt uniform sampling across $S_{\delta}$ to capture violations comprehensively.
# Experiment Validating $\alpha$-$\beta$-$\epsilon$ Relationship
To empirically validate this relationship, we conducted an experiment in the Boat Navigation case study (Sec. 4.1). Figure 1 (https://shorturl.at/VYYai) illustrates:
- Safety error rate ($\alpha$) computed as $\alpha = \frac{k+1}{N_s+1}$ (Purple).
- Theoretical safety violation probability ($\epsilon$) derived from Equation (14) (Orange).
- Empirical safety violation probability, estimated via sampling 3 million initial states and simulating their rollouts (Green).
We use $N = 300K$ and $\beta = 10^{-10}$. We note that empirical violation rates consistently remain below theoretical bounds, confirming the validity of our approach.
# Setting $\alpha = 1$ and Circumventing Conformal Prediction
We acknowledge that setting $\alpha = 0$ (zero violations) indeed eliminates the need for conformal prediction. To test this, we mark the black point in Figure 1 above that corresponds to $\alpha = 0$ and $\delta$ level of $-0.3234$, yielding nearly 100\% safety. As expected, this approach reduces the volume of the resulting safe set, but we still obtain a sizable safe set that accounts for worst-case violations, as suggested by the reviewer. In contrast, $\delta = 0$ achieves ~99.9\% safety, reducing conservatism but at a slight safety compromise. In this sense, our framework can be viewed as a robust generalization of this extreme-case approach, offering users the flexibility to choose their preferred level of conservatism based on the application's safety-performance requirements.
# Relevant $\epsilon$ and $\beta$, if quantity in eq(15) Accumulate Over Time
Since all the analysis is performed for the entire trajectory starting from a given state, $\epsilon$ and $\beta$ already account for time accumulation.
# Additional Baselines
We kindly refer the reviewer to the discussion on additional baselines with reviewer: Rqif.
# Essential References Not Discussed
We appreciate the reviewer’s suggestion and will include [1] in the revised manuscript.
[1] Hsu et al. The safety filter: A unified view...
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Rebuttal Comment 1.1:
Comment: I was really excited to read your rebuttal and to see the way my comments were thoroughly addressed.
While I'm still not sure about the i.i.d assumption and would encourage the Authors to further think about it (that is, balancing safety and efficiency may put the trajectories close to the boundaries of the safe set), the empirical evidence provided by the Authors confirms the theory, at least, on the considered task.
With that, I am raising my score. Thanks for all the good work!
---
Reply to Comment 1.1.1:
Comment: Thank you for your thoughtful feedback and for increasing your score! We appreciate your detailed comments and are glad that our clarifications addressed your concerns. Your constructive engagement has been invaluable, and we look forward to further refining our work based on your insights. | Summary: This paper proposes a novel Physics-Informed framework to address the co-optimization problem of safety objectives and performance objectives for Constrained Reinforcement Learning (CRL). The paper reformulates the co-optimization problem as a state-constrained optimal control problem (SC-OCP) with epigraph formulation. Moreover, the authors propose an algorithmic approach to learning the SC-OCP value function from which the policy is induced. At last, this paper proposes a conformal prediction-based verification strategy to provide a probabilistic guarantee of safety and performance degradation. The proposed framework is demonstrated on several nonlinear control tasks.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Partially, I checked all equations and theoretical statements except for the proofs for Theorem 3.2
Experimental Designs Or Analyses: Yes.
Supplementary Material: No supplementary material was found in the submission.
Relation To Broader Scientific Literature: The proposed contributions are related to Constrained Reinforcement Learning.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. The targeted problem is well-motivated, and the solution is novel.
2. The reformulation of the CRL problem is insightful, and the derived physics-informed loss function for the learning value function is mathematically sound.
3. The theoretical analysis and empirical study support the claimed contributions.
Weaknesses:
1. Some technical details need more clarification. Please see the questions
Other Comments Or Suggestions: Please see the questions.
Questions For Authors: 1. How is the policy $\pi_\theta$ synthesized? The searched policy should minimize equation 11; however, how the policy is learned is unclear. The authors should provide more details, such as what algorithm is used and how policy is parameterized.
2. How is the parameter $\lambda$ determined in equation 10? How does $\lambda$ affect the safety and performance? It would be nice if the authors could provide more insights.
3. To achieve a high probabilistic guarantee, the proposed verification methods need to densely sample the state space (300K), which is non-trivial. Can you provide more discussion on the practicality and potential limitations of real-world applications?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # How is the policy $\pi_{\theta}$ synthesized?
The final policy $\pi_{\theta}(t, x)$ is synthesized by first determining the optimal $z^*$ by solving the following optimization problem for any $(t,x)$:
\begin{equation}
\begin{aligned}
z^* = &\arg\min_{z \in \mathbb{R^+}} \; z \\
\text{s.t.} & \; \hat{V}_{\theta}(t,x,z) \leq \delta,
\end{aligned}
\end{equation}
For efficiency purposes, we solve the above optimization problem via binary search on $z$.
Once $z^*$ is determined, the optimal control policy is the policy that minimizes the Hamiltonian ($H(t,\hat{x})$) [1] at the corresponding augmented state $(x, z^*)$, denoted as $\hat{x}^*$:
\begin{equation}
H(t,\hat{x}^*) = \min_{u\in \mathcal{U}} \langle\nabla \hat{V}_{\theta}(t, \hat{x}^*), \hat{f}(\hat{x}^*, u)\rangle.
\end{equation}
This results in the final policy $\pi_{\theta}$, as provided in Equation (17) of the submitted manuscript:
\begin{equation}
\pi_{\theta}(t,x) = \arg \min_{u\in \mathcal{U}} \langle\nabla \hat{V}_{\theta}(t, \hat{x}^*), \hat{f}(\hat{x}^*, u)\rangle.
\end{equation}
Intuitively, the policy $\pi_{\theta}$ at any state $x$ follows the minimum cost path, which is given by the gradient descent direction of the auxiliary value function.
The overall policy inference process takes $2ms$ on our standard GPU system.
# How is the parameter $\lambda$ determined in equation 10? How does it affect the safety and performance?
For a given partial differential equation (PDE), multiple solutions may exist, and uniqueness is ensured only when an appropriate boundary condition is imposed. The parameter $\lambda$ regulates the enforcement of this boundary condition. If $\lambda$ is too small, the boundary function may not be adequately learned, resulting in an inaccurate solution. To address the sensitivity of the learned solution to $\lambda$, we employ the adaptive loss restructuring approach from [2], which dynamically updates $\lambda$ at each iteration. The updates are directly proportional to the ratio of the boundary loss gradient to the PDE loss gradient. Intuitively, a small ratio results in a lower $\lambda$, prioritizing the PDE loss, whereas a larger ratio increases $\lambda$, emphasizing boundary condition enforcement.
# To achieve a high probabilistic guarantee, the proposed verification methods need to densely sample the state space (300K), which is non-trivial. Can you provide more discussion on the practicality and potential limitations of real-world applications?
The work [3] by Vovk states that a smaller number of samples leads to greater fluctuations in the conformal prediction calibration, meaning that if we redraw $N$ samples and repeat the conformal prediction process, we might get a different calibration result.
This variance decreases as $N$ increases.
Similarly, in our work, a small $N$ means that the value correction term $\delta$ might fluctuate each time the verification algorithm is executed. Therefore, to ensure a stable estimate of $\delta$, it is desirable to select a sufficiently large value of $N$.
Additionally, Figure 1 in https://shorturl.at/8vgih presents the $\alpha-\epsilon$ plots for varying numbers of verification samples $N$ and different values of $\beta$. From the figure, we observe that as $N$ increases, the effect of $\beta$ diminishes, and the curve approaches the $\alpha = \epsilon$ line. Ideally, the user-specified safety error rate ($\alpha$) should closely match the safety violation parameter ($\epsilon$) while maintaining high confidence ($1-\beta$ close to 1).
Thus, selecting a larger $N$ enables a smaller $\beta$ while ensuring the alignment of $\alpha$ and $\epsilon$. Conversely, if $N$ is small, one must either compromise on the confidence parameter $\beta$ or accept that $\alpha$ will be lower than $\epsilon$, resulting in a more conservative upper bound on the safety rate.
**References**
[1] S. Bansal, M. Chen, S. Herbert, and C. J. Tomlin, "Hamilton-Jacobi reachability: A brief overview and recent advances," 2017 IEEE 56th Annual Conference on Decision and Control (CDC), Melbourne, VIC, Australia, 2017, pp. 2242-2253, doi: 10.1109/CDC.2017.8263977.
[2] S. Wang, Y. Teng, and P. Perdikaris, “Understanding and mitigating gradient flow pathologies in physics-informed neural networks,” SIAM Journal on Scientific Computing, vol. 43, no. 5, pp. A3055–A3081, 2021.
[3] V. Vovk, “Conditional validity of inductive conformal predictors,”
2012. [Online]. Available: \\ https://arxiv.org/abs/1209.2673 | Summary: The paper addresses the challenge of simultaneously optimizing performance and safety in autonomous systems by formulating it as a state-constrained optimal control problem. The key contribution is a physics-informed machine learning (PIML) framework that efficiently approximates the Hamilton-Jacobi-Bellman (HJB) equation, capturing the optimal value function under hard safety constraints. By embedding known system dynamics into the learning process, the approach mitigates the computational challenges of solving HJB equations in high-dimensional settings. Additionally, the authors introduce a conformal prediction-based verification method to quantify learning errors and provide probabilistic safety guarantees. The learned value function is statistically corrected to ensure safety with a high-confidence bound, and a separate conformal prediction step quantifies potential performance degradation. Empirical evaluations on three autonomous control tasks demonstrate that the framework learns controllers that maintain safety constraints while achieving near-optimal performance.
## update after rebuttal
I thank the authors for their response. My questions have been largely answered. New baselines and experimental results for scalability are appreciated and will make a good addition to the paper. For the new safe RL baselines, please include experimental results for all tasks in the paper. I updated my overall recommendation accordingly.
Claims And Evidence: Most claims in the paper are reasonable and supported by empirical results.
The authors claim that their framework scales to complex, high-dimensional systems where classical Hamilton-Jacobi (HJ) or grid-based methods become computationally infeasible. While their experiments include tasks with moderately high-dimensional state spaces, they provide limited discussion or formal analysis on how the approach would extend to even higher-dimensional problems, as encountered in some real-world robotic applications). A deeper investigation into scalability limits, such as computational complexity or the effects of increasing dimensionality on solution accuracy, would strengthen this claim.
Methods And Evaluation Criteria: The proposed method is well-motivated for the problem at hand. The authors reformulate the state-constrained optimal control problem in epigraph form, introducing an auxiliary value function that incorporates an additional state variable. This enables the problem to be solved using a Hamilton-Jacobi-Bellman (HJB) approach, leveraging physics-informed machine learning to approximate solutions efficiently.
**Baselines**:
The chosen benchmark tasks are reasonable but could be expanded (see "Experimental Designs or Analyses" for details).
However, the baseline selection could be improved. The current baselines include:
- C-SAC and MPPI, which are soft-constrained methods that do not enforce strict safety.
- MPPI-CBF, which introduces a hard safety constraint but is the only explicitly safe baseline.
While MPPI-CBF provides a useful comparison, a single safe baseline is insufficient to fully assess the method’s safety-performance tradeoffs. Additionally, soft-constrained baselines like C-SAC may not be the best comparison since they treat safety as a penalty rather than a hard constraint, potentially ignoring safety violations rather than actively enforcing constraint satisfaction.
To strengthen the evaluation, the authors should consider safe reinforcement learning baselines that explicitly handle hard constraints, such as: Constrained Policy Optimization (CPO), Interior-Point Policy Optimization (IPO).
These methods dynamically adjust constraint handling (e.g., by tuning Lagrange multipliers) and would provide a more rigorous safety comparison.
**Evaluation Metrics**:
The evaluation is based on cumulative cost (to measure performance), and safety rate (percentage of trajectories that remain safe). While these metrics are relevant, they are not sufficient to fully characterize the safety-performance tradeoff. Some limitations include:
- Cumulative cost does not explicitly account for constraint satisfaction trade-offs, i.e., two methods with similar costs might differ significantly in how well they satisfy safety constraints.
- Safety rate provides only a binary measure so it does not capture the severity or frequency of constraint violations (e.g., how far a trajectory enters an unsafe region).
Additional metrics could provide deeper insights, such as:
- Constraint violation magnitude: Quantifying how much and how often safety constraints are violated.
- Worst-case safety violations: To ensure the method does not fail catastrophically in rare but critical scenarios.
- Computational efficiency: Since the approach is meant to scale, measuring inference time or sample efficiency would strengthen claims about scalability.
Theoretical Claims: The paper presents several theoretical claims, primarily related to the Hamilton-Jacobi-Bellman (HJB) formulation, epigraph reformulation, and conformal prediction-based verification. While I am not deeply familiar with the theoretical aspects of this work, I have outlined some potential areas for further scrutiny. My suggestions may not be fully comprehensive.
The conformal prediction-based safety verification (Theorem 3.1) and performance quantification (Theorem 3.2) leverage results from distribution-free uncertainty quantification. These rely on assumptions about the distribution of sampled states, and their applicability to high-dimensional control problems could benefit from additional discussion.
The method learns the HJB solution using a physics-informed neural network. Theoretical guarantees on convergence or approximation error bounds for the learned solution are not explicitly discussed, which could impact scalability and accuracy in high-dimensional settings.
Experimental Designs Or Analyses: The experiments primarily involve 2D environments, likely due to the assumption of known system dynamics. While these tasks are reasonable for evaluating safety constraints, incorporating higher-dimensional agents (e.g., quadrupeds like Ant from Safety Gym) would better assess scalability and applicability to more complex scenarios.
Task 2 (Pursuer-Evader) is unclear. The description refers to an "evader vehicle," but the visualizations appear to show pursuer vehicles interacting with humans. This raises several questions:
- What exactly is the task? Is the pursuer meant to collide with the evader, follow it at a safe distance, or something else?
- If the goal is to track the evader, what defines successful tracking?
- Does the pursuer ever need to prioritize obstacle avoidance over tracking?
Additionally, the environment complexity could be increased to better challenge the proposed method. Consider scenarios where:
- More obstacles block the direct path to the target.
- The free space is more constrained (e.g., narrow passages), requiring more precise maneuvering under safety constraints.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The use of epigraph reformulation to enforce hard constraints and conformal prediction for probabilistic safety verification appears to be a novel combination that extends prior work in safe reinforcement learning. A deeper comparison with safe RL methods (e.g., Constrained Policy Optimization, Interior-Point Policy Optimization) and HJ-reachability-based safety filtering could help clarify how this approach advances the state of the art.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: __Strengths__:
- The epigraph formulation effectively transforms the constrained problem into an augmented state space, facilitating tractable optimization.
- Theoretical guarantees for safety verification and performance quantification strengthen the framework’s reliability.
__Weaknesses__:
- Solving high-dimensional HJB Partial Differential Equations (PDEs) remains computationally expensive, limiting real-time applicability.
- Assumes known (or well-learned) system dynamics, restricting applicability to environments with uncertain or evolving dynamics.
- Limited comparison against strong safe control baselines, reducing the robustness of empirical validation.
- Experimental tasks are relatively simple, likely due to the dependence on known dynamics, limiting generalizability to more complex settings.
Other Comments Or Suggestions: Task 2 description can be rephrased (see my comments above).
Questions For Authors: - How does the learned auxiliary value function $\hat{V}$ compare to Control Barrier Functions in ensuring safety? Can it be directly used as a CBF, or how would it integrate with CBF-based methods? A response clarifying this relationship would help assess whether the approach can be leveraged in existing safety-critical control frameworks.
- How well does the proposed framework transfer to more complex, high-dimensional systems with unknown or highly nonlinear dynamics? Have you tested it beyond the benchmark tasks? Demonstrating broader applicability would strengthen the paper’s impact.
- If the assumed or learned system dynamics deviate significantly from reality, how does the approach perform in terms of both safety and optimality? Have you evaluated it under model uncertainty or system disturbances? A discussion on this would clarify the method’s robustness in real-world deployment.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Clarification regarding the Pursuer Evader Problem
In the Pursuer-Evader case study (Section 4.2), the objective is for a pursuer robot to chase a moving target and reach as close to this target as possible within the time horizon. The human figure serves only as a placeholder for the evader and can be substituted with any other entity (e.g., another robot). The key aspect of the problem is the interaction between the pursuer and the evader, both of which follow the dynamics outlined in Appendix B.2. The quality of tracking is encoded by the performance cost, which at each time step is equal to the $l_2$ distance between the evader and the pursuer. The lower the cumulative performance cost, the better the quality of tracking. In addition to tracking, the pursuer needs to avoid collisions with obstacles, which is encoded as a safety constraint. Due to this constraint, the pursuer indeed needs to prioritize obstacle avoidance over tracking at times. An example of this is shown in Figure 1 (anonymous link: https://shorturl.at/gWIrw). Here, the pursuer vehicle can achieve a lower tracking cost by cutting through the obstacle; however, due to the collision-avoidance constraint, the pursuer goes around the obstacle and intercepts the evader from behind.
# Comparison with Other Safe RL Baselines
In response to reviewer suggestions, we benchmarked our method against additional safe RL baselines: CPO [1], IPO [2], and PPO-Lagrangian [3] on the Pursuer-Evader problem. Our results are summarized below:
| Method | Safety Rate (%) | % Cost Higher than Our Method |
|------------------|-----------------|-------------------------------|
|CPO|75.11| 123.14|
|IPO|72.3 |110.34|
|PPO-Lag|63.33|114.63|
These experiments reveal that although CPO and IPO achieve marginally higher safety rates compared to C-SAC, all safe RL baselines underperform compared to the proposed approach in both safety and cost metrics.
# Scalability of the Proposed Method
We assess the computational scalability of the proposed approach by reporting offline and online computation times across 3 case studies:
| Task | Dim | Offline Time | Online Time |
|------------------------|----------------|--------------|-------------|
| Boat Navigation|2|122 min|2 ms|
| Evader Chasing|8|195 min|2 ms|
| Multi-Agent Navigation|20|323min|2 ms|
Traditional grid-based methods exhibit exponentially scaling computation complexity and become intractable for higher-dimensional problems (8D and 20D). In contrast, our method shows only a modest increase in the offline computation time when going from a 2D to a 20D system while maintaining real-time inference (2 ms) across all dimensions—a key advantage for real robotic applications.
# Relations to Control Barrier Functions (CBFs)
The learned auxiliary value function, $\hat{V}$, captures a notion of safety similar to CBFs. In particular, the condition $\hat{V}(x,z) \leq 0$ defines the safe region for the system, while $\hat{V}(x,z) > 0$ corresponds to unsafe states-mirroring the core idea behind CBFs. Therefore, $\hat{V}(x,z)$ can directly serve as a CBF for the system.
However, importantly, $\hat{V}(x,z)$ extends beyond standard CBFs by also capturing performance objectives. Through the parameter $z$, one can modulate the trade-off between safety and performance, effectively generating a family of CBF-like functions with different safety-performance characteristics. As a result, $\hat{V}$ can serve as a CBF in traditional settings or be integrated into CBF-based safety frameworks to encode both safety and performance objectives.
# Tackling Model Uncertainty/Disturbances
We discuss the extension of the proposed approach to account for model uncertainty and disturbances in our rebuttal to reviewer BKAj. Due to space constraints, we respectfully refer the reviewer to that discussion for further details.
# Transfer to Complex, High-Dimensional Systems
The primary goal of this work is to lay the foundation for integrating PINNs with HJ Reachability to co-optimize safety and performance in autonomous systems. Our framework already demonstrates strong potential for high-dimensional applications, as evidenced by its success in a 20D multi-agent navigation task. Moreover, the safety constraints in our experiments are also highly complex—often consisting of disconnected, non-convex sets—highlighting the method's ability to handle intricate safety specifications. Further extension and testing of our framework on more complex systems is an exciting future research direction.
# References
[1] Achiam, J. et al. (2017). Constrained Policy Optimization. *ICML*.
[2] Liu, Y. et al. (2020). IPO: Interior-point Policy Optimization under Constraints. *AAAI*.
[3] Ray, A. et al. (2019). Benchmarking Safe Exploration in Deep Reinforcement Learning. *arXiv preprint*.
[4] Bansal, S. et al. (2017). Hamilton-Jacobi Reachability: A Brief Overview and Recent Advances. *IEEE CDC*. | null | null | null | null | null | null |
Moirai-MoE: Empowering Time Series Foundation Models with Sparse Mixture of Experts | Accept (poster) | Summary: The authors propose an MoE extension to an existing Time series based foundation model MOIRAI. The authors extends the standard Moirai to MoE to reduce the dependency on human-imposed frequency decomposition as it is not a reliable grouping of pre-training data. They claim that different frequencies can display similar patterns and similar frequencies can display different patterns. Instead the authors use a sparse MoE approach so that the model can learn the groupings. The authors perform an extensive evaluation and show that their approach results in SOTA performance. The paper is well written and provides clear motivation - this paper is a valuable addition to the scientific community.
## update after rebuttal
After considering the response from the authors - my recommendation remains accept. The work is of merit and useful to the ICML community.
Claims And Evidence: The authors claim that an MoE approach removes the human-imposed frequency decomposition within the MOIRAI model such that the model itself learns the appropriate token clustering. The claims are well founded and the authors provide clear intuition behind their rationale - as seen in Figure 1. Additionally, the authors clearly demonstrate the SOTA performance of their method which further backs up their approach. The claims stated in the paper are well backed up by the evaluation.
Methods And Evaluation Criteria: The proposed method is clearly motivated and the evaluation is comprehensive - 39 datasets and current state of the art time-series FMs.
The core idea of MOIRAI-MOE is to exclude human-defined time series groupings while delegating the modeling of diverse time series patterns to the sparsely activated experts in Transformer layers. The authors also investigate existing expert gating functions that generally use a randomly initialized linear layer for expert assignments. They introduce a new expert gating function for accurate expert assignments and improved performance. The author propose automatic time series token-level specialisation, where diverse tokens are handled by different experts, while similar tokens share parameter space, reducing learning complexity. MoE is done by replacing every FFN by an MoE layer consisting of M experts and a Gating function G. The evaluation criteria used is well motivated and comprehensive.
Theoretical Claims: No theoretical claims were made in the paper
Experimental Designs Or Analyses: The authors use a comprehensive and appropriate experimental design consisting of relevant datasets and other SOTA time-series foundation models.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper is of clear interest to time-series forecasting and advancing the current SOTA with respect to time-series Foundation models. The impact of such research is of high significance and impact to the wider scientific community due to the application of time-series forecasting.
Essential References Not Discussed: No
Other Strengths And Weaknesses: A weakness of this study is around the evaluation of the probabilistic forecasting component of the paper - which I think is more valuable than the deterministic evaluations performed. The results are indeed impressive but a statistical analysis of the probabilistic forecasting performance and characteristics would be a valuable addition to this well motivated study.
Other Comments Or Suggestions: One typo on line 213: "Mo" should be "MoE"
Questions For Authors: 1) The authors argue that different frequencies can display similar patterns and similar frequencies can display different patterns - which I agree with. However could some wavelet transformation/layer not alleviate this issue within the standard architecture?
2) No adaptive patching was considered in the method - so how are different resolutions considered if at all?
3) The authors perform mini-batch k-means clustering on the attention outputs to continuously update the cluster centroids at each layer where the cluster number is equal to the number of experts - did you observe any discrepancies doing this such as the number of clusters being significantly different to the number of experts?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **[C1] A weakness of this study is around the evaluation of the probabilistic forecasting component of the paper - which I think is more valuable than the deterministic evaluations performed. The results are indeed impressive but a statistical analysis of the probabilistic forecasting performance and characteristics would be a valuable addition to this well motivated study.**
We provide standard deviations and statistical significance in Table 1 at this link: https://drive.google.com/file/d/1bwJ7dyji_OnSNkYXpA6IOpwnvF6nOZmS/view
**[C2] The authors argue that different frequencies can display similar patterns and similar frequencies can display different patterns - which I agree with. However could some wavelet transformation/layer alleviate this issue within the standard architecture?**
Thank you for the insightful comment. Indeed, applying a wavelet transformation in the input space can effectively help identify and distinguish patterns in time series. However, pattern specialization of Moirai-MoE are performed at each Transformer layer, and this allows our model to adaptively capture patterns at various hierarchical abstraction levels throughout the model. This hierarchical and adaptive specialization provides greater flexibility and modeling power compared to a static transformation applied at the input. Nevertheless, your suggestion of integrating wavelet transformations into the input is intriguing, and further experimentation would be valuable to empirically evaluate and compare the performance.
**[C3] No adaptive patching was considered in the method - so how are different resolutions considered if at all?**
Thank you for your comment. We would like to clarify that different resolutions are considered equivalent in our context, as we use a uniform patch size. The critical factor in our approach is the pattern or shape of the time series data, and the specialization of the model primarily addresses this aspect of diversity. Additionally, we have already included experiments examining the effects of different patch sizes in the appendix. The results show that the choice of patch size 16 works the best.
**[C4] The authors perform mini-batch k-means clustering on the attention outputs to continuously update the cluster centroids at each layer where the cluster number is equal to the number of experts - did you observe any discrepancies doing this such as the number of clusters being significantly different to the number of experts?**
Thank you for the insightful question. This question depends on the relative values of the cluster number K and the number of experts E, and we address it in two parts:
Case 1: K smaller than E — This setting is not valid in our framework. Since each cluster corresponds to an expert during MoE training, having fewer clusters than experts would result in multiple experts sharing the same cluster centroid. This leads to repeated expert selections and undermines the intended diversity and specialization of the experts.
Case 2: K larger than E — This is a more interesting scenario. For example, when K=64 and E=32, we face the challenge of mapping the 64 cluster centroids to the 32 experts. A practical and effective strategy we adopt is as follows: for each token (data point), we compute its distance to all 64 centroids, and select the top 32 centroids with the smallest average distances across tokens. These selected centroids are then used during MoE training. Despite having more clusters than experts, this approach still allows us to select the most representative centroids for expert routing.
We validated this approach experimentally. Results show that this method achieves comparable performance to the standard setting where K equals to E, indicating that even with a larger number of clusters, a careful selection mechanism can yield effective and robust MoE behavior. | Summary: This paper proposes MOIRAI-MOE, a time series foundation model based on the Mixture of Experts (MoE). It replaces the traditional frequency-grouping strategy with data-driven token-level specialization, thus addressing the pre-training challenges posed by the high heterogeneity of time series data. The model achieves significant performance improvements on 39 datasets by introducing an expert routing mechanism based on the clustering centers of pre-trained dense models and an autoregressive prediction objective.
Claims And Evidence: Claims are supported by in-distribution/zero-shot results in Tables 3, 6, and 8, which show MOIRAI-MOE’s superiority in MAE, CRPS, and other metrics. Ablation studies demonstrate that MoE specialization, not just the decoder objective, drives performance gains.
Methods And Evaluation Criteria: The sparse MoE efficiently scales model capacity while maintaining computational efficiency. Cluster Gating improves load balancing and expert relevance compared to random initialization.
The evaluation uses diverse datasets (Monash, zero-shot benchmarks) and metrics (MASE, CRPS), ensuring robustness.
Theoretical Claims: Theoretical derivations (e.g., MoE layer formulation, gating function) are standard and correctly applied. However, the theoretical grounding (e.g., convergence guarantees) of the cluster-based gating mechanism is not explicitly proven.
Experimental Designs Or Analyses: This paper includes baseline comparisons of both foundation models (MOIRAI, Chronos) and specialized models (PatchTST). Meanwhile, ablation studies isolate the impact of MoE, gating, and pretraining objectives. Moreover, the efficiency analysis in Table 4 shows comparable inference speeds to MOIRAI despite larger total parameters.
Supplementary Material: Appendices provide dataset details, full results, and visualizations, which can strengthen the main claims.
Relation To Broader Scientific Literature: Builds on MOIRAI (Woo et al., 2024) by replacing frequency projections with MoE. Extends sparse MoE from language/vision (Fedus et al., 2022) to time series. Compares favorably with concurrent work Time-MoE (Shi et al., 2024) by introducing cluster gating and patch tokenization.
Essential References Not Discussed: No critical omissions noted. The paper comprehensively cites relevant works like TimesFM, Chronos, and existing MoE literature.
Other Strengths And Weaknesses: Strengths:
1. This paper proposed a new model architecture, which introduces a Sparse Mixture of Experts (MoE) to dynamically route tokens to specialized experts, overcoming the limitations of human-defined frequency grouping.
2. The proposed method proposes a novel gating mechanism using cluster centroids from pre-trained dense models, outperforming randomly initialized linear routing.
3. The proposed method achieves superior performance, which outperforms state-of-the-art baselines (e.g., MOIRAI, Chronos) on 39 datasets, reducing MAE by up to 17% with the same activated parameters and surpassing others with 65× fewer activated parameters.
Weaknesses:
1. Analysis in Fig. 6 reveals some experts in deeper layers are rarely activated, indicating inefficient parameter usage. While pruning is mentioned as future work, no concrete solution is provided.
2. The proposed clustering-based routing relies heavily on pre-trained MOIRAI, which introduces a dependency on the quality of the pre-trained model and dataset (LOTSA), and thus potentially limiting generalization to domains outside the pretraining distribution.
3. MOIRAI-MOE contains significantly more parameters than those of MOIRAI. This increases memory demands during training and deployment. Is it possible to use model compression technology to reduce the parameters of the model?
4. When MOIRAI-MOE and MOIRAI parameters are equivalent, how does MOIRAI-MOE perform?
5. While outperforming foundation models, MOIRAI-MOE still lags behind fully fine-tuned specialized models like TiDE on some datasets (e.g., ETT1 in Table 8), indicating room for improvement in extreme domain adaptation.
Other Comments Or Suggestions: N/A
## update after rebuttal
While the authors have addressed certain technical concerns (e.g., pruning validation and training cost metrics) with additional clarifications, some limitations around generalizability dependencies and methodological novelty remain unresolved. Though the reviewer leans toward maintaining the original score, the paper's demonstrated empirical improvements and structured rebuttal make a case for acceptance, depending on broader reviewer consensus.
Questions For Authors: See weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **[C1] While pruning is mentioned as future work, no concrete solution is provided.**
Thanks for the comment. A concrete pruning solution is to first evaluate expert usage by tracking gating activations during pretraining. Identify experts with significantly fewer activations (e.g., activated less than 1\% of total gating decisions) as underutilized. Completely remove these expert modules from the model architecture, thereby reducing GPU memory usage. Lastly, update the gating network accordingly to ensure it routes inputs correctly to the remaining experts.
**[C2] The proposed clustering-based routing relies heavily on pre-trained MOIRAI, which introduces a dependency on the quality of the pre-trained model and dataset (LOTSA), and thus potentially limiting generalization to domains outside the pretraining distribution.**
Regarding the argument about "potentially limiting generalization to domains outside the pretraining distribution": This challenge is inherent to all time series foundation models, not solely Moirai-MoE. Therefore, it underscores the importance of assembling a comprehensive and diverse time series pretraining corpus to maximize coverage of potential application domains.
Regarding the argument on the "dependency on the quality of the pretrained model": We acknowledge this dependency. Indeed, recent advancements in MoE-based Large Language Models (such as Qwen1.5-MoE) explicitly leverage pretrained dense models to introduce beneficial inductive biases, thereby enhancing model performance. Consequently, we consider this dependency a strategic strength rather than a limitation. Our work aligns with this research direction, with the assumption of a high-quality pretrained model and focusing on effectively leveraging it to achieve further performance gains.
**[C3] MOIRAI-MOE contains significantly more parameters than those of MOIRAI. This increases memory demands during training and deployment. Is it possible to use model compression technology to reduce the parameters of the model?**
The increase in parameter count of Moirai-MoE does not proportionally affect computational cost during inference because, at any given time, only a subset of the experts are activated. However, model compression techniques can indeed be leveraged to reduce the parameters: (1) By converting weights from full precision (e.g., FP32) to lower precision (e.g., INT8 or FP16), quantization techniques can substantially reduce memory footprint while maintaining accuracy. (2) Techniques such as knowledge distillation can transfer learned representations from a larger Moirai-MoE model to a smaller, compressed model, thus achieving efficiency without a significant loss in performance.
Implementing these compression techniques individually or in combination could mitigate memory concerns associated with Moirai-MoE. We will explore integrating these strategies into our framework and evaluate their impact on model performance and efficiency in subsequent research. Thank you for the suggestion.
**[C4] When MOIRAI-MOE and MOIRAI parameters are equivalent, how does MOIRAI-MOE perform?**
Our current configuration is as follows: Moirai-Base has a total of 91M parameters, while Moirai-MoE-Small has 117M parameters. To address your concern, we introduce a variant of Moirai-MoE-Small, called Moirai-MoE-Small-V2, by reducing the FFN dimension. This variant has a total parameter count of 89M, which is closely aligned with that of Moirai-Base.
We pretrain Moirai-MoE-Small-V2, evaluate it on the 29 datasets of the Monash benchmark, and compute the aggregated performance. Note that the aggregated MAE of Moirai-Base is 0.71 (according to Figure 3 in the main paper), while Moirai-MoE-Small-V2 achieves an aggregated MAE of 0.67, demonstrating superior performance.
**[C5] MOIRAI-MOE still lags behind fully fine-tuned specialized models like TiDE on some datasets (e.g., ETT1 in Table 8), indicating room for improvement in extreme domain adaptation.**
We believe there might be some misunderstanding. We carefully compare the performance of TiDE and Moirai-MoE on the ETT1 dataset in Table 8. The CRPS and MASE of TiDE are 1.056 and 6.898, while the CRPS and MASE of Moirai-MoE-Small are 0.288 and 1.750. Since lower values are better, Moirai-MoE-Small is actually significantly better than TiDE on this dataset.
However, to address your concern, we do find that on the Walmart dataset, TiDE performs better than Moirai-MoE-Small: TiDE scores 0.077 for CRPS and 0.814 for MASE, while Moirai-MoE-Small scores 0.090 for CRPS and 0.927 for MASE. This is a case where Moirai-MoE requires fine-tuning for better domain adaptation. After fine-tuning Moirai-MoE-Small, the results improve to 0.071 for CRPS and 0.756 for MASE, successfully surpassing TiDE.
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Rebuttal Comment 1.1:
Comment: Thank you for the authors' response. However, I find that my key concerns remain largely unaddressed and I will maintain my original score, detailed in the following:
**Re. for C1:**
Although the authors discussed a potentially viable pruning method, which removed the underutilized branches. However, it is only a very common and simplistic pruning paradigm. The authors did not consider how pruning specifically applies to time series models, nor how to mitigate the severe performance degradation that may result from pruning.
**Re. for C2:**
I acknowledge that “this challenge is inherent to all time series foundation models,” and indeed, it is an important issue that needs to be addressed. The proposed method, which is based on pre-trained MOIRAI, does not consider how to tackle this challenge, thus limiting the overall effectiveness of the approach.
**Re. for C3:**
The authors claim that “the increase in parameter count of Moirai-MoE does not proportionally affect computational cost during inference.” However, the computational and memory costs during training are also crucial. In general, the authors did not provide concrete measurements of computational or storage cost, either during training or inference. Therefore, their explanation is not sufficiently convincing.
**Re. for C4:**
I noticed that MOIRAI-MoE-Small (117M parameters) has significantly more parameters than MOIRAI-Small (only 14M), indicating that the MoE mechanism introduces a substantial increase in parameter count. The authors compared MOIRAI-MoE-Base with MOIRAI-MoE-Small, which is an unfair comparison. Furthermore, whether the MoE architecture introduces additional computational overhead should be discussed in more detail.
Therefore, I will keep the original rating.
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Reply to Comment 1.1.1:
Comment: Dear reviewer, we would like to express our sincere thanks for the time you have taken to review our submission, and thank you very much for responding our rebuttal. Please find our further responses below.
**[C1] Although the authors discussed a potentially viable pruning method, which removed the underutilized branches. However, it is only a very common and simplistic pruning paradigm. The authors did not consider how pruning specifically applies to time series models, nor how to mitigate the severe performance degradation that may result from pruning.**
Thank you very much for raising this point. After our initial response four days ago, we implemented the discussed pruning method, pretrained the resulting model, and evaluated its performance on the 29 datasets from the Monash benchmark. So the aggregated results are now available and they show that the pruned Moirai-MoE-Small achieves an aggregated MAE of 0.66, which is comparable to the original Moirai-MoE-Small’s aggregated MAE of 0.65. These outcomes are reasonable, as underutilized experts do not contribute to the model's capabilities, meaning their removal does not negatively impact overall performance.
**[C2] I acknowledge that “this challenge is inherent to all time series foundation models,” and indeed, it is an important issue that needs to be addressed. The proposed method, which is based on pre-trained MOIRAI, does not consider how to tackle this challenge, thus limiting the overall effectiveness of the approach.**
Thank you for your comment. The overall effectiveness of Moirai-MoE has been thoroughly validated through comprehensive evaluations on 39 datasets, outperforming state-of-the-art baselines (e.g., Moirai, Chronos, TimesFM). The challenge mentioned in our current discussion pertains primarily to the comprehensiveness of our pretraining dataset, LOTSA. This issue relates more directly to the coverage of the pretraining corpus rather than to methodological considerations, placing it somewhat outside the intended scope of our current paper. Our work focuses explicitly on methodological advancements, specifically enhancing the Moirai model architecture through our proposed Moirai-MoE architecture. Therefore, we kept the pretraining corpus fixed as a controlled factor to demonstrate and discuss improvements attributed solely to the methodological innovation.
**[C3] The computational and memory costs during training are also crucial. In general, the authors did not provide concrete measurements of computational or storage cost, either during training or inference.**
Thank you for raising this point. We provided inference cost details in Table 4 of our paper, but we acknowledge that the training cost details were not fully addressed. To clarify the computational and memory costs during training, we inspect the pretraining logs and provide the following information:
We utilized 16 GPUs to pretrain both Moirai and Moirai-MoE models. Specifically: (1) Moirai-MoE-Small required 9.49 hours of pretraining for 50,000 steps, with a peak memory usage of 14.52 GB per GPU. (2) Moirai-Small took 4.69 hours to pretrain for 50,000 steps, with a peak memory usage of 11.45 GB per GPU. The difference in pre-training time and memory usage is due to the difference in the total number of parameters between Moirai-Small (14M) and Moirai-MoE-Small (117M).
**[C4] The authors compared MOIRAI-MoE-Base with MOIRAI-MoE-Small, which is an unfair comparison. Furthermore, whether the MoE architecture introduces additional computational overhead should be discussed in more detail.**
Thank you for your comment. In our initial rebuttal, we explicitly stated that our comparison is between Moirai-Base (91M) and Moirai-MoE-Small-V2 (89M), which is fair, given their similar parameter counts. We did not compare Moirai-MoE-Base and Moirai-MoE-Small in our initial response. Your concern about the computational cost associated with the MoE architecture is outlined above in the response to [C3].
Thank you again for your constructive feedback. We hope our additional clarifications address the concerns and would greatly appreciate if you could reconsider the rating. | Summary: This paper introduces a novel foundational model for time series forecasting, building upon the architecture of Moirai. The primary motivation is to address a key limitation of existing time series foundational models, which rely on manually imposed clustering—such as specialized layers for different time series structures (e.g., frequency-based clustering in Moirai). Instead, the authors propose an automated approach using a mixture of experts (MoE) to dynamically detect dataset diversity and automatically cluster heterogeneous patterns within the pretraining data. Additionally, rather than using conventional MoE layers, which are sensitive to initialization, the authors introduce a clustering-based method that enhances robustness. Experimental results on multiple datasets demonstrate the effectiveness of the proposed approach compared to existing methods.
Claims And Evidence: Key claims of the authors with comments
**Improved Token-Level Clustering**
Moirai-MoE enables automatic and more efficient token-level clustering compared to Moirai, which relies on human-defined frequency-based clustering. Figure 5 illustrates how Moirai-MoE performs data-driven clustering. However, there is no empirical evidence showing that this clustering is interpretable by humans. The appendix should include more visualizations, highlighting cases where clustering does or does not align with human intuition. Additionally, testing on synthetic datasets with clear clustering structures could help formally validate this approach. For example, experiments could assess clustering uniqueness in homogeneous datasets or evaluate whether Moirai-MoE correctly identifies imposed structures in datasets with predefined clusters. Stronger empirical evidence is needed.
**Improved Expert Gating in MoE**
Moirai-MoE enhances MoE by introducing a clustering-based expert gating mechanism, addressing the sensitivity issue in traditional MoE architectures. Figure 4 presents an ablation study comparing this gating method to standard linear projection. While the experiments support this claim, further validation is needed. Running multiple trajectories with different initializations could help assess the stability of clustering beyond performance improvements. Additionally, reporting standard deviations would strengthen the claim regarding Moirai-MoE’s robustness.
**State-of-the-Art (SOTA) Performance Across Benchmarks**
The authors conduct extensive benchmarking against multiple competitors and datasets. However, incorporating statistical tests, such as reporting standard deviations and statistical significance, would better demonstrate the stability and reliability of the proposed approach.
Methods And Evaluation Criteria: **Relevant Benchmark Datasets**
The authors primarily use the Monash dataset, which is increasingly recognized in the time series literature, making it a sensible choice for benchmarking.
**Valid Methodological Approach**
The proposed methods are well-founded, as they address data heterogeneity—a key challenge in time series foundational models.
Theoretical Claims: The manuscript does not provide a theoretical guarantee for the proposed method. To enhance its quality, the authors might conduct a theoretical analysis comparing clustering-based MoE to linear mapping. Even in a simplified setting—where each expert is linear—they could analyze how a student MoE approximates a teacher MoE under both architectures (for examples). This would provide deeper insights into the model’s theoretical foundations. But this is more a suggestion than a criticize.
Experimental Designs Or Analyses: **Experimental Results & Reproducibility**
The experimental results demonstrate computational efficiency and good performance, but several improvements might improve the manuscript.
A. Statistical Validation
- As previously mentioned, incorporate standard deviations where necessary.
- Perform statistical tests to confirm the stability of the approach.
B. Reproducibility & Transparency
- Clearly explain how results were collected (e.g., best epochs for validation/test/train, last epoch for in-distribution experiments).
- Provide a detailed explanation of how "out-of-distribution" data is defined and ensure no data leakage occurs.
- Include algorithmic details (Mainly in algorithm environment) in the manuscript to facilitate reproducibility.
C. Visualization of Zero-Shot Forecasting
- Include additional visualizations (at least in the appendix) showcasing zero-shot forecasting results even though some are given but not compared with competitors.
- Specifically, highlight both successes and failures, explaining where Moirai fails and why, as well as where it succeeds (or Moirai-MoE) and the underlying reasons.
Supplementary Material: I roughly through all the supplementary materials but not in details.
Relation To Broader Scientific Literature: **MoE in Time Series Foundational Models** – *Weak Contribution*
The incorporation of MoE is not a significant contribution, as it has already been used in Time-MoE. While the authors highlight some differences, the novelty remains limited.
**New Expert Gating with Clustering** – *Moderate Contribution*
This contribution is moderately novel, as such expert gating has not been previously proposed. However, the lack of theoretical evidence and extensive experimental validation weakens the claim of its stability.
Essential References Not Discussed: No essential references to mention
Other Strengths And Weaknesses: **Strengths**
- Addressing data heterogeneity is a valuable approach, and the use of MoE appears to be a promising solution.
- The paper includes extensive experiments across multiple datasets, demonstrating thorough evaluation.
- The writing is clear, making the paper easy to follow.
**Weaknesses**
- The contributions are somewhat moderate, as several prior works have already explored MoE for time series (e.g., Time-MoE).
- There is a lack of strong theoretical justification and limited empirical evidence regarding the stability of the expert gating system.
Other Comments Or Suggestions: All suggestions have been written before
Questions For Authors: **On the expert gating**
Instead of using a direct clustering approach for expert gating, introducing a third loss (a clustering loss) in the embedding space could be beneficial. This would encourage natural grouping of similar patterns without requiring an explicit, manually determined clustering step. A contrastive loss (e.g., a soft clustering loss or DeepCluster-like approach) could be used to enforce structure in the learned representation. This avoids the need for a preliminary run of Moirai with a single layer, making the process more automated and adaptive. Have you considered loss functions like InfoNCE or DeepCluster for this purpose?
**Computational Comparison with Moirai**
- Training Complexity:
Moirai already reduces the sample size by clustering, but if clustering is done implicitly through a loss function rather than manually, the computational overhead may shift from pre-processing to training.
If the gating mechanism remains data-dependent, backpropagation complexity might increase due to additional constraints in the loss function.
- Inference Complexity:
If expert selection remains soft, inference might require evaluating multiple experts per sample, increasing computation time.
Could you comment about time complexity and memory complexity of the algorithm and illustrate that empirically.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **IMPORTANT: Figures 1, 2, 3 and Tables 1, 2 are provided here: https://drive.google.com/file/d/1bwJ7dyji_OnSNkYXpA6IOpwnvF6nOZmS/view**
**[C1] Testing on synthetic datasets with clear clustering structures. Assess clustering uniqueness in homogeneous datasets or evaluate whether Moirai-MoE correctly identifies structures in datasets with predefined clusters.**
We generate synthetic datasets with basic time series patterns to assess the ability of Moirai-MoE in a controllable way. The resulted visualization is in Figure 1.
**[C2] Include zero-shot visualizations, highlight both successes and failures, explaining where Moirai fails and why**
We conducted additional visualizations comparing Moirai-MoE-Small with Chronos-Small and TimesFM, as shown in Figures 2 and 3. Figure 2 illustrates failure cases for Moirai-MoE—these time series primarily exhibit trend without seasonality. In such cases, both Moirai-MoE-Small and Chronos-Small perform poorly, while TimesFM performs exceptionally well. However, we suspect possible data leakage in TimesFM, as its forecasts align almost perfectly with the future trend, which we believe could be inherently unpredictable. Figure 3 presents success cases where Moirai-MoE outperforms the others. Its forecasts are generally closer to the ground truth, whereas Chronos-Small and TimesFM tend to show larger overestimations or underestimations. Due to word count limitations at the rebuttal stage, we present only two cases here, but we will add more cases and analyses in the appendix of the manuscript.
**[C3] Reporting standard deviations and statistical significance would better demonstrate the stability and reliability of the proposed approach**
Standard deviations and statistical significance are in Tables 1 and 2.
**[C4] Clearly explain how results were collected (e.g., best epochs for validation/test/train, last epoch for in-distribution experiments)**
Moirai-MoE is pretrained for a certain number of epochs on a large time series corpus. After pretraining, the checkpoint saved from the last epoch is used to perform inference on 29 in-distribution datasets. Based on the aggregated performance, we know the optimal number of epochs required to achieve the best in-distribution performance and then we use this checkpoint for zero-shot evaluation.
**[C5] Provide explanation of how "out-of-distribution" data is defined and ensure no data leakage occurs.**
We follow the settings of the well-recognized time series foundation models (TSFMs), such as Moirai, Chronos, and TimesFM, the out-of-distribution data refers to those datasets (including their training, validation, and test sets) that are not included in the pretraining corpus.
**[C6] The contributions are somewhat moderate. The incorporation of MoE is not a significant contribution, as it has already been used in Time-MoE.**
We would like to argue our position from the following points. First, although Time-MoE has applied MoE to TSFMs, its application has not demonstrated superior effectiveness, as evidenced by its inferior zero-shot forecasting performance. In our zero-shot evaluations, its performance significantly trails behind Moirai-MoE. It does not even surpass Moirai-Large, as demonstrated in both our zero-shot evaluations and the point forecasting results over 27 datasets reported by the Chronos Team (https://aws.amazon.com/blogs/machine-learning/fast-and-accurate-zero-shot-forecasting-with-chronos-bolt-and-autogluon/). Hence, our contribution lies not merely in applying MoE to TSFMs but, importantly, in achieving notably superior performance compared to Time-MoE. Second, we have dedicated considerable effort to exploring and understanding the internal mechanisms of MoE models. This depth of analysis has not been previously addressed in the literature, including the Time-MoE study. Thus, this should be recognized as a meaningful contribution of our paper.
**[C7] Have you considered InfoNCE or DeepCluster for this purpose? Could you comment about time complexity and memory complexity.**
We appreciate the suggestion regarding the integration of clustering-based losses, such as InfoNCE or DeepCluster, into MoE training. We also find your provided training and inference complexity analysis reasonable. While these methods could indeed offer a more automated approach to structuring representations, their effectiveness might not be guaranteed in practice. Imposing clustering losses during MoE training could introduce optimization challenges and potentially interfere with the primary learning objectives of the model. Our current approach adopts a two-stage process. This separation offers training stability, particularly in the early stages when representations may not be sufficiently structured for effective contrastive learning. Our method can also leverage the inductive bias from the pretrained Moirai model. Nevertheless, we consider your recommendation a valuable and promising direction for future exploration.
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Rebuttal Comment 1.1:
Comment: I would like to thank the author for their detailed comments and thorough evaluation. Empirically, the results are quite interesting, even though the performance gap compared to competitors like TimesFM and Chronos remains somewhat limited. Nonetheless, the empirical efforts are valuable, and the results could be of interest to the community, which is why I have decided to maintain my score as "weak accept."
However, I find the methodology to be somewhat empirical, with limited theoretical justification and strong empirical evidence, aside from the motivation for automatic clustering. Additionally, the contribution feels moderate, with the exception of the promising results that are claimed.
From my perspective, the key strengths of the method lie in the good empirical results across different datasets and the motivation behind automatic clustering. However, I feel that the theoretical investigation and the underlying intuitions are not fully developed, which limits the potential for broader impact within the community together with the limited contribution which is a bit incremental.
For these reasons, I am keeping my score unchanged. | Summary: The paper focuses on the pretraining of time series foundation models using large time series corpora.
The paper argues that there are significant drawbacks to current approaches that address heterogeneity by grouping time-series based on human-identified features such a frequency. The paper proposes an alternative that involves using a sparse mixture of experts (MoE) that provides an avenue towards automatic specialization. The paper reports results for multiple datasets, demonstrating outperformance of the selected baselines. Experimental analysis is included that explores the operation of the MoE foundation models.
--AFTER REBUTTAL
I thank the authors for their thoughtful response. I was somewhat surprised that there was no response to my follow-up questions about the routing mechanism and the very sparse utilization of experts. The authors addressed three of my initial concerns, providing good responses. In particular, they emphasized the value of the engineering effort in getting an MoE time-series foundation model to work and they reported variability for some experiments. The authors pointed out that I had misinterpreted the gating mechanism and that it was non-trainable. But understanding this, the follow-up question in my response to the rebuttal was how the non-trainable router differed from a clustering-based hash approach that has been proposed previously. There was no response to this. The authors were claiming this as a significant novel technical contribution of the paper, so the lack of justification is concerning. The other residual concern was how uneven the usage of the experts was. I had concerns about the design approach given that it emerges that only a handful of the experts are being used at higher layers in the architecture. Given that these concerns were not addressed, I will retain my score (weak reject).
Claims And Evidence: Please see "Other Strengths and Weaknesses"
Methods And Evaluation Criteria: Please see "Other Strengths and Weaknesses"
Theoretical Claims: Please see "Other Strengths and Weaknesses"
Experimental Designs Or Analyses: Please see "Other Strengths and Weaknesses"
Supplementary Material: I attempted to check the code, but many of the files in the repository appear to be corrupted.
I read through all appendices.
Relation To Broader Scientific Literature: Please see "Other Strengths and Weaknesses"
Essential References Not Discussed: Please see "Other Strengths and Weaknesses"
Other Strengths And Weaknesses: Strengths
S1. The paper proposes to augment a foundational time series model (MOIRAI) with a sparse Mixture-of-experts. The key innovation is a novel strategy to pre-train the experts, which involves clustering tokens according to the attention outputs of an inference model. There is also a carefully executed tokenization strategy.
S2. The paper reports the results of extensive experiments. These demonstrate that the MoE approach achieves a significant performance improvement over the base MOIRAI models, even when there are far fewer active parameters.
S3. The paper conducts a good experimental analysis to provide insights into how the MoE is behaving (e.g., how different frequencies are assigned to different experts at different layers of the model). There are useful visualizations and thorough investigations in the appendices. The paper includes ablation studies as well as studies of the sensitivity to different design choices and parameter settings.
Weaknesses
W1. The technical contributions of the paper are relatively minor. There is some adjustment of the token construction process, but this appears to be more of an engineering exercise to make the operation and training efficient. Beyond this, the primary novel technical contribution is the use of the token clusters during the pre-training of the MoE, with the clustering based on the attention outputs of an inference model. While this is an innovative solution, and a welcome acknowledgement of the challenge of successfully training a sparse MoE, the technical content is presented in 13 lines of text and a single equation. Overall, while there are some innovative contributions, the paper seems to be a relatively straightforward application of existing sparse MoE techniques to MOIRA, with some careful engineering effort to ensure that the training is successful.
W2. The paper claims to introduce “a new expert gating function for accurate expert assignments and improved performance”. This claim does not seem to be supported, as I cannot detect a significant difference between the proposed gating and the procedure in Shazeer et al, 2017. There is novelty in the pretraining based on clusters but this does not imply a new gating function – the claim is misleading. A more correct claim would be “we introduce a novel procedure for pre-training the gating function in a standard sparse mixture-of-experts model”.
W3. The paper does not report variability for any of the experiments and there are no confidence intervals. There are no statistical significance tests.
Other Comments Or Suggestions: None
Questions For Authors: Q1. Figures 5 and 6 (and 9 in the appendix) show why expert allocation is important. This paper uses a standard Sparse-MoE setup with all experts having the same structure. If trained and regularised correctly, allocation should be approximately uniform (like Fig. 7 in Mixtral). While it is desirable to have some experts focused on specific frequencies, Figure 6 suggests that many experts are not contributing at all. This is also confirmed by Figure 9 in the Appendix. Although the token clusters approach achieves the best performance, these results suggest that the training is not operating correctly. It suggests some form of representation collapse. Was this investigated by the authors?
[R1] Jiang, Albert Q., et al. "Mixtral of experts." arXiv preprint arXiv:2401.04088 (2024).
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **[C1] Code repository are corrupted.**
The issue appears to be related to viewing the files directly through the web interface. We verify that downloading the repository locally resolves the issue.
**[C2] The paper seems to be a relatively straightforward application of existing sparse MoE techniques to MOIRAI, with some careful engineering effort to ensure that the training is successful.**
Regarding the argument "the token construction process is more of an engineering exercise to make the operation and training efficient; with some careful engineering effort to ensure that the training is successful". In fact, efficiency is a crucial aspect, particularly when developing Time Series Foundation Models (TSFMs). TSFMs typically have large parameter sizes and require training on large time series corpus, making efficiency critical. Notably, the paper you referenced (Shazeer et al., 2017) uses an entire section (Section 3) to discuss efficiency challenges in training MoE models, including considerations such as batch size, model parallelism, and network bandwidth. These discussions are engineering-focused—arguably even more so than our paper—but does that diminish their importance or exclude them from being considered technical contributions?
Regarding the argument "the paper seems to be a relatively straightforward application of existing sparse MoE techniques". While it may sound easy to apply existing MoE techniques to TSFMs, making these techniques effective in practice is challenging. Our work represents a pioneering effort in successfully adapting sparse MoE to TSFMs. How do we define success in this context? An intuitive and primary criterion for success is the downstream model performance. For instance, the concurrent work Time-MoE, can hardly be considered successful, as its performance significantly trails behind Moirai-MoE. Notably, Time-MoE does not even surpass Moirai-Large, as demonstrated in both our zero-shot evaluations and the point forecasting results over 27 datasets reported by the Chronos Team (https://aws.amazon.com/blogs/machine-learning/fast-and-accurate-zero-shot-forecasting-with-chronos-bolt-and-autogluon/). In summary, while a straightforward application of existing MoE techniques to TSFMs may seem easy, achieving SOTA performance is technically non-trivial and depends critically on model design.
Finally, as you acknowledged in the strengths part, we have put significant effort into the behavior of MoE models. This area of investigation has not been explored in the literature, including the Time-MoE work. Thus, this should be recognized as a meaningful contribution of our paper.
**[C3] Cannot detect a significant difference between the proposed gating and the procedure in Shazeer et al, 2017. A more correct claim would be “we introduce a novel procedure for pre-training the gating function in a standard sparse mixture-of-experts model”.**
Your suggested point is reasonable in certain respects; however, we would like to emphasize that the paper you mentioned (Shazeer et al., 2017) employs a linear projection as its gating, which relies on a randomly initialized, trainable weight matrix for expert assignment. In contrast, Moirai-MoE utilizes a gating function that is non-trainable and initialized based on clustering results from a pretrained model, not randomly. We believe this distinction marks a departure from the linear projection gating, effectively constituting a new gating function. We would appreciate further clarification regarding which aspects you consider identical between these two gating functions.
**[C4] No confidence intervals and statistical tests.**
Standard deviations and statistical significance are in Table 1: https://drive.google.com/file/d/1bwJ7dyji_OnSNkYXpA6IOpwnvF6nOZmS/view
**[C5] Although the token clusters approach achieves the best performance, these results suggest that the training is not operating correctly.**
Thank you for your comment. We do not believe our training is incorrect. Our routing mechanism is based on clustering results derived from a pretrained Moirai model's representations. If certain clusters exhibit similarity, the selection of experts would be naturally constrained, resulting in some experts being underutilized. Thus, the question here pertains to the representation similarity inherent in pretrained TSFMs. Existing research has investigated representation similarities within TSFMs. A recent study (https://arxiv.org/pdf/2409.12915v2) uses Centered Kernel Alignment to measure representation similarity, highlighting clear redundancy in TSFMs such as Chronos and Moirai. Additionally, another study (https://arxiv.org/pdf/2302.11939v2), specifically Section 7, reports that within-layer token similarity tends to increase in deeper Transformer layers. This finding aligns closely with our own observations in Moirai-MoE, where fewer experts are activated due to increased token similarities, particularly in deeper layers. | null | null | null | null | null | null |
Towards Theoretical Understanding of Sequential Decision Making with Preference Feedback | Accept (poster) | Summary: This paper considers sequential decision making with preference feedback. The authors build a theoretical formulation linking preferences, utilities (i.e., non-Markovian rewards), and Markovian rewards, and then study the connections between them. First, the authors model preference feedback using a partial (pre)order over trajectories, which enables the presence of incomparabilities. Second, the authors study how a preference relation can be approximated by a multi-objective utility. They introduce a notion of preference-utility compatibility and analyze the computational complexity of this transformation, showing that constructing the minimum-dimensional utility is NP-hard. Third, the authors propose a new concept of preference-based policy dominance that does not rely on utilities or rewards, and analyze the computational complexity of assessing it. Fourth, the authors develop a computationally efficient algorithm to approximate a utility using (Markovian) rewards, and quantify the error in terms of the suboptimality of the optimal policy induced by the approximating reward. This paper aims to lay a foundation for sequential decision making from preference feedback, with promising potential applications in RL from human feedback.
Claims And Evidence: The claims made in this paper are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria make sense.
Theoretical Claims: The theoretical results look reasonable, but I didn’t go through every proof.
Experimental Designs Or Analyses: There is no experiment in this paper.
Supplementary Material: I didn’t read the supplementary material.
Relation To Broader Scientific Literature: This paper is relevant to the literature.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
1. This paper proposes a theoretical formulation which links preferences, utilities (i.e., non-Markovian rewards), and Markovian rewards, and then study the connections between them.
2. The authors model preference feedback using a partial (pre)order over trajectories and propose a new notion of preference-based policy dominance. In addition, the authors study the computational complexity of the transformation and assessment for the proposed notions in this preference-based and utility-based MDP formulation.
Weaknesses:
1. The writing and readability of this paper should be improved. This paper is hard to follow. The abstract is a bit long.
2. This paper seems to be a pure theoretical work, which defines a MDP based on partial order and proves some of its properties. What is the motivation of the proposed MDP formulation based on partial order and utility? How can this MDP formulation relate and contribute to real-world applications, e.g., the RL with human feedback and LLM applications?
3. There is no new algorithm proposed, and there is no experiment. The contribution is purely theoretical, i.e., a new MDP formulation defined based on partial order and utility, which is limited.
Other Comments Or Suggestions: Please see the weaknesses above.
Questions For Authors: Please see the weaknesses above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the Reviewer for the time spent reviewing our paper. Below, our answers to the Reviewer's comments and concerns.
> The writing and readability of this paper should be improved. This paper is hard to follow. The abstract is a bit long.
We thank the Reviewer for raising this point. We will make our best efforts to improve the readability of the paper, in particular for Sections 2 and 5, also leveraging the additional available page. We commit to improve it by lightening the notation (moving the not fundamental one to the appendix) and rewriting some parts which are less fluid.
> This paper seems to be a pure theoretical work, which defines a MDP based on partial order and proves some of its properties. What is the motivation of the proposed MDP formulation based on partial order and utility? How can this MDP formulation relate and contribute to real-world applications, e.g., the RL with human feedback and LLM applications?
> There is no new algorithm proposed, and there is no experiment. The contribution is purely theoretical, i.e., a new MDP formulation defined based on partial order and utility, which is limited.
We thank the Reviewer for raising the point. We believe that our theoretical formulation of preference-based MDP (especially with partial orders) is **strongly motivated by real-world applications**. We provide arguments for this statement below:
1. In the real-world, a **preference feedback is a much more realistic feedback than both rewards (used in RL) and demonstrations (used in Inverse RL)**. Consider, for example, LLM applications: it is quite natural of a human to state which of two proposed answers they prefer, rather than trying to define a reward function for answer generation, or asking the human to demonstrate which answer they would want to receive.
2. Furthermore, it is as realistic to consider that **a human might not be able to state a clear preference between any pair of proposed trajectories**. Regarding LLM applications, if we were to ask a human to state their preference between two answers, the human may evaluate different aspects, e.g., the length, the clarity, the correctness, and the harmfulness of the answers. Thus, it is possible that the human may not be able to state a clear preference. This requires modeling **incomparabilities** among trajectories. One natural approach to address this need is to consider **partial order relations** among trajectories. Another example is the well-known problem of autonomous driving, where we want to balance terms of travel time and travel comfort. Clearly, these two objectives are in contrast, as reckless driving brings the passenger to the destination quicker but at the cost of their comfort, whereas a completely comfortable drive may take too much time to reach the destination. By considering a partial order relation over trajectories, we are able to capture the multi-dimensionality of such a problem. The preference-based MDP (PbMDP) framework we propose in this paper allows us to formally define these problems.
3. Finally, having motivated **why** we need a framework to generalize preferences to allows for incomparabilities, we ask **what** we are able to learn. Thus, we propose novel concepts of **dominance between policies**, and study the computational complexity of evaluating them. The NP-completeness results we propose constitute a computational barrier on **what** is possible to ask of a (practical) algorithm. Then, we study a way to approximate this problem, rendering it computationally tractable, at the cost of an approximation error.
We will leverage the additional page to include a discussion on this point, as we recognize the importance of motivating a novel framework from real-world applications. | Summary: This paper establishes a rigorous theoretical framework for sequential decision-making with preference feedback, where agents learn from comparative evaluations of trajectories rather than explicit reward signals. The authors make several key contributions:
1. They model preference feedback using partial preorders between trajectories, enabling the formal characterization of incomparability phenomena that occur when trajectories cannot be meaningfully ranked.
2. The research investigates systematic approaches to approximate preference relations using multi-objective utility functions.
3. The authors develop a novel concept of preference-based policy dominance that operates independently of utility functions or rewards.
4. They present an algorithm that efficiently approximates utilities using Markovian rewards, complete with quantifiable error bounds.
Together, these contributions create a principled framework connecting preferences, utilities, and Markovian rewards in sequential decision-making environments.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: This is a pure theory paper.
Theoretical Claims: I have reviewed the high-level proof idea and did not find obvious issues.
Experimental Designs Or Analyses: This paper contains no experiments.
Supplementary Material: No.
Relation To Broader Scientific Literature: These results build upon previous work in theoretical computer science/game theory and provide new findings for RLHF.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Strengths**
- The paper establishes a comprehensive framework that connects preferences, utilities, and rewards in sequential decision-making, filling an important gap in the theoretical understanding of preference-based learning.
- Unlike many existing approaches, the authors explicitly model preferences as partial preorders, allowing for incomparabilities that commonly occur with human preferences but are often overlooked in the literature.
- The work provides valuable insights into the computational complexity of various transformations between preferences, utilities, and rewards, highlighting fundamental challenges in this domain.
**Weaknesses**
- Some theoretical results largely follow or implied by existing known results (e.g., Theorem 4.2). While this work offers new insights for decision making with preference feedback, highlighting the technical novelty of the proof would further strengthen the paper.
- While establishing a solid theoretical foundation, the paper places less emphasis on developing practical algorithms that could be immediately applied to real-world problems.
- The paper is purely theoretical, with no empirical evaluation to validate how well the proposed methods perform in practice compared to existing RLHF methods. This limitation is significant for such an application-driven area.
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Overall, I appreciate the new theoretical framework developed by the authors and would advocate for acceptance.
Other Comments Or Suggestions: na
Questions For Authors: na
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the Reviewer for the time spent reviewing our work and we appreciate the Reviewer's understanding of the relevance of the proposed framework. Below, our answers to the Reviewer's comments.
> Some theoretical results largely follow or implied by existing known results (e.g., Theorem 4.2). While this work offers new insights for decision making with preference feedback, highlighting the technical novelty of the proof would further strengthen the paper.
While we recognize that some of the results, especially those presented in Section 4, can be obtained with non-complex arguments starting from existing ones, **they have never been presented in the literature, as far as we know**. Concerning the **technical novelty**, we report below two examples of results we present that bring technical novelty:
- Theorem 5.4: its proof involves a reduction to a non-standard NP-complete problem of **topological ordering in weighted DAG** (Gerbner et al., 2016) which requires a non-trivial construction.
- Theorem 6.1: it **generalizes the bisimulation lemmas** from the case of a scalar utility (or reward) to the case of multi-dimensional utilities. This requires defining a proper index to evaluate suboptimality on the Pareto frontier, which is the function $\mathcal{L}(\boldsymbol{u},\boldsymbol{\widehat{u}})$.
We have rewritten the Original Contribution paragraph to better highlight these aspects.
> While establishing a solid theoretical foundation, the paper places less emphasis on developing practical algorithms that could be immediately applied to real-world problems.
> The paper is purely theoretical, with no empirical evaluation to validate how well the proposed methods perform in practice compared to existing RLHF methods. This limitation is significant for such an application-driven area.
We take the liberty to answer both questions together since our choices are justified by a specific aim. Preference-based RL and/or RLHF is, as the Reviewer notes, "such an application-driven area". However, the understanding of the intimate properties of the preference relations is currently missing. This paper precisely aims to **make a step forward the understanding of the theoretical properties of preference relations** and its limitations (that are significant, as we show) from a computational perspective. This, in our view, represents a fundamental step to, for instance, avoid that practitioners attempt to address problems which turn out to be provably hard (e.g., checking policy dominance for partial orders). This is the reason why we decided not to (1) propose algorithms and (2) conduct an experimental validation. Clearly, building on our work, and aware of the computational limitations, future works should formalize real-world problems according to this setting, and design algorithms capable of solving them, under **certain assumptions**, to achieve convenient computational (and, subsequently, statistical) guarantees.
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Rebuttal Comment 1.1:
Comment: Thank you for your response. I believe these clarifications will improve the paper. I will maintain my positive score. | Summary: The authors consider the setting of sequential decision-making problems in which only preferences over trajectories are provided, specifically partial (pre)orders. This allows for situations where comparisons of pairs of trajectories are not available (incomparabilities). After several definitions to precisely capture this setting, including the notion of utility-preference compatibility, the authors show how a multiobjective utility function can be constructed from the preorder and that constructing the utility function with the smallest dimensionality is NP-hard. Finally, the authors propose a quadratic program to approximate such a utility function with a reward function for an approximate MDP and provide a bound on the incurred error.
Claims And Evidence: I followed the proofs and could not find any mistakes but this is not my area of expertise.
Methods And Evaluation Criteria: There are no evaluations involving examples or simulations.
Theoretical Claims: I followed the proofs and could not find any mistakes but this is not my area of expertise.
Experimental Designs Or Analyses: No experiments were conducted.
Supplementary Material: I worked through all the proofs in the supplementary material.
Relation To Broader Scientific Literature: This is not my area of expertise, and I am not knowledgeable enough about preference-based RL and RL from human feedback. I was wondering about any potential canonical problems and datasets that could be used to construct Markovian reward functions solving the quadratic program (eq. 13) and thereby providing a sense of the applicability of the present algorithm and the value of the provided error bound.
Essential References Not Discussed: As for inverse RL, I was surprised that the authors did not cite work that directly connects preference elicitation and inverse reinforcement learning.
Other Strengths And Weaknesses: This is a theoretical paper that makes notions of utility-preference compatibility, policy dominance, and the connection between partial preorders on trajectories, utility functions, and reward functions in an approximate MDP precise, shows that establishing policy dominance in the very general case considered here is NP-hard, and provides a constructive algorithm for reward functions in an approximate MDP. This relates to preference-based RL and RL from human feedback.
It is difficult for me to assess how much of an advancement in the field this is, as I am not an expert in this area.
Other Comments Or Suggestions: “in the realizer ofthe"
Questions For Authors: Are there any problems and datasets that could be used to construct Markovian reward functions solving the quadratic program (eq. 13) and thereby provide a sense of the applicability of the present algorithm and the value of the error bound?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the Reviewer for the time spent reviewing our work, for understanding the relevance of the QP and of the error bound. Below, our answers to the Reviewer's questions.
> As for inverse RL, I was surprised that the authors did not cite work that directly connects preference elicitation and inverse reinforcement learning.
We thank the Reviewer for raising this point. We have not included methods specific to the Inverse RL field in the related works of this paper due to the following reasoning:
1. **IRL focuses on observing a behavior** that is assumed to be optimal and learning a reward function, whereas, according to our framework, we consider the case in which the **agent interacts with the environment, asking for preference feedback** to be used to estimate a reward and to improve its policy. For this reason, the two frameworks are different;
2. Preference elicitation and IRL are related to the learning aspect of the problem, and, thus, to the statistical complexity of doing so, whereas, in this work, we focus on the different concepts of optimality and the computational complexity of estimating multi-dimensional utility and reward functions. In other words, we focus more on **computational complexity** rather than on **statistical complexity**. As we briefly discuss in the future works, one possible direction is to address learning with preference feedback when incomparabilities are possible. When tackling such a direction, it will then be necessary to compare with the literature of preference elicitation and IRL.
However, we acknowledge that there exist works that combine both preference elicitation and IRL, such as (Rothkopf and Dimitrakakis, 2011). We added a discussion on this in the related works.
Rothkopf, C. A., and Dimitrakakis, C. Preference elicitation and inverse reinforcement learning. ECML-PKDD 2011.
> Are there any problems and datasets that could be used to construct Markovian reward functions solving the quadratic program (eq. 13) and thereby provide a sense of the applicability of the present algorithm and the value of the error bound?
In principle, existing RL benchmarks could be adapted to accomodate the problem of solving the QP to estimate an approximated reward function. This can be done either by querying preference from real humans (see, e.g., Christiano et al., 2017) or by defining a synthetic expert (see, e.g., Akrour et al., 2012). One example of existing datasets which can be adapted to allow for incomparabilities are those based on the OpenAI Gym, which can be found in Minari (https://minari.farama.org/main/), from the Farama Foundation.
Regarding LLMs, there exist datasets which, with the necessary adaptations, could be considered for what the Reviewer suggests. One such example is the *Preference Dissection* dataset (Li et al., 2024), which contains questions, pairs of answers, and features for each answer. Although the reported human preferences do not admit incomparabilities, synthetic preferences could be generated considering the answers and their features. An additional example is the *PKU-SafeRLHF* dataset (Ji et al., 2024), which contains questions and answers labelled in terms of harmfulness and correctness. Again, it would be necessary to generate synthetic preferences.
In conclusion, we believe that the definition of a standardized benchmark containing both standard RL tasks and language tasks, together with human-labelled datasets and synthetic parametric experts would be beneficial for the evaluation of future approaches to the problem of learning from preferences with incomparabilities.
Christiano, P. F., Leike, J., Brown, T., Martic, M., Legg, S., and Amodei, D. Deep reinforcement learning from human preferences. NeurIPS 2017.
Akrour, R., Schoenauer M., and Sebag M. April: Active preference learning-based reinforcement learning. ECML-PKDD 2012.
Li, J., Zhou, F., Sun, S., Zhang, Y., Zhao, H., and Liu, P. Dissecting human and llm preferences. arXiv preprint arXiv:2402.11296, 2024.
Ji, J., Hong, D., Zhang, B., Chen, B., Dai, J., Zheng, B., Qiu, T., Li, B., and Yang, Y. PKU-SafeRLHF: Towards Multi-Level Safety Alignment for LLMs with Human Preference. arXiv preprint arXiv:2406.15513, 2024. | Summary: This paper aims to build a theoretical basis linking the preference-based MDP, the utility-based MDP, and the reward-based MDP. Specifically, this paper formulates these three settings in Section 3, and discusses the connections between the preference-based MDP and the utility-based MDP in Section 4. In Section 5, this paper discusses the dominance and optimality with preferences; and finally, in Section 6, it discusses the relationship between the utility-based MDP and the reward-based MDP.
Claims And Evidence: To the best of my knowledge, the claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: This paper does not have any experiment results.
To the best of my knowledge, the theoretical claims (theorems) in this paper seem to be correct.
Theoretical Claims: I have checked the proofs in a high level. To the best of my knowledge, the proofs seem to be correct.
Experimental Designs Or Analyses: Not applicable.
Supplementary Material: I have checked the proofs in a high level.
Relation To Broader Scientific Literature: This paper has done a good job of literature review. However, I have some concerns about the novelty and significance of this paper, which I will list below.
Essential References Not Discussed: To the best of my knowledge, No.
Other Strengths And Weaknesses: I have some concerns about the novelty and significance of this paper. Specifically,
1) It seems that some parts of this paper are well-known results from the classical choice theory and existing work, such as Theorem 4.2. Might the authors clearly explain in the rebuttal what are the new results of this paper and what are the existing results?
2) My understanding is that this paper has discussed many different issues related to preference-based MDPS, utility-based MDPs, reward-based MDPs, as well as their connections. Several theorems have been developed; however, it seems that none of them is very hard to prove, and none of them is really counter-intuitive. This might reduce the significance of this paper.
In addition, from the perspective of writing, this paper is mathematically too heavy, and is not easy to read.
Other Comments Or Suggestions: This paper has done a good job of literature review.
Questions For Authors: Please try to address the questions/weaknesses listed above.
-----------------------------------------------
I have read the authors' rebuttal, which has addressed some of the concerns listed above, especially the concerns about the novelties and technical contributions of this paper. I will increase my recommendation from 2 to 3.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the Reviewer for the time spent reviewing our work. Below, our answers to the Reviewer's questions and concerns.
> It seems that some parts of this paper are well-known results from the classical choice theory and existing work, such as Theorem 4.2. Might the authors clearly explain in the rebuttal what are the new results of this paper and what are the existing results?
To the best of our knowledge, **all the results presented in the paper are novel**. While we recognize that some of them, especially those presented in Section 4, can be obtained with non-complex arguments starting from existing ones, they have never been presented in the literature, as far as we know. Specifically, considering Theorem 4.2, while it is known that **computing the order-dimension is NP-hard** (Yannakakis, 1982), we claim that also **computing a minimal compatible utility is NP-hard**. This is proved with a simple, we recognize, but still novel, **reduction** to the problem of computing the order-dimension. We kindly ask the reviewer to provide references that already report any of the results we provide in this paper.
We refer the Reviewer also to the itemize in the answer below for further discussion.
> My understanding is that this paper has discussed many different issues related to preference-based MDPS, utility-based MDPs, reward-based MDPs, as well as their connections. Several theorems have been developed; however, it seems that none of them is very hard to prove, and none of them is really counter-intuitive. This might reduce the significance of this paper.
We honestly **disagree with the Reviewer on the fact that if a theorem is "not very hard to prove" or "really counter-intuitive" then this reduces its significance**. Beside being quite subjective notions, we wonder how many papers accepted at top-conferences (like ICML) really contain theorems that are "very hard to prove" and "really counter-intuitive". Just think to the bandit literature where the regret bound is often known before proving it (not counter-intuitive) and the proofs follow minor variations of techniques established by 20 years (not very hard to prove). Nevertheless, we report below two examples of theorems, in our opinion, that are either counter-intuitive or hard to prove:
- Theorem 5.1: is *counter-intuitive* since it is not obvious that the condition of Definition 5.1, which involves an **existential quantification** over the compatible utilities (which are an infinite continuous set), can be verified by checking a finite number of inequalities.
- Theorem 5.4: is *not simple to prove* since it involves a reduction to a non-standard NP-complete problem of **topological ordering in weighted DAG** (Gerbner et al., 2016) which requires a non-trivial construction. Furthermore, in the authors' opinion, the fact that checking policy dominance in a partial order is NP-complete is quite *counter-intuitive*.
Moreover, there are results that are significant beyond this work. For example, Theorem 6.1 generalizes the **bisimulation lemmas** from the case of a scalar utility (or reward) to the case of multi-dimensional utilities. This requires defining a proper index to evaluate suboptimality on the Pareto frontier (function $\mathcal{L}(\boldsymbol{u},\boldsymbol{\widehat{u}})$).
> In addition, from the perspective of writing, this paper is mathematically too heavy, and is not easy to read.
We thank the Reviewer for raising the point. We will make our best efforts to improve the redability of the paper, in particular for Sections 2 and 5, also leveraging the additional available page. We commit to improve it by lightening the notation (moving the not fundamental one to the appendix) and rewriting some parts which are less fluid.
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Rebuttal Comment 1.1:
Comment: Thanks for the rebuttal and clarifications. The rebuttal has partially addressed my concerns, especially my concerns on the novelties and technical contributions of this paper. I will increase my overall recommendation to 3. | null | null | null | null | null | null |
Regret-Free Reinforcement Learning for Temporal Logic Specifications | Accept (poster) | Summary: The paper tackles reinforcement learning (RL) under linear temporal logic (LTL) specifications in unknown Markov decision processes (MDPs). The primary goal is to guarantee sublinear regret with respect to the (unknown) optimal probability of satisfying an LTL property. From classic reach-avoid setting, author also extend to a more general setting using LTL property to a deterministic Rabin automaton.
Claims And Evidence: Claims are all supported by solid proof and toy example experiment backup.
Methods And Evaluation Criteria: Methods and evaluation criteria make sense. Since this approach is under tabular MDP setting, experiment seems fairly easy but the major contribution is on the theory side.
Theoretical Claims: I have walked through proof of thm 4.4 which makes sense to me, but I'm curious of the definition of transition function in eq4.
Experimental Designs Or Analyses: Yes, the experiment makes sense under the basic tabular setting. However, it would be great if author can conduct experiments on more complex setting, eg. more complicated map?
Supplementary Material: I have checked the proof and supplementary experiments.
Relation To Broader Scientific Literature: This work borrows idea from classic controller synthesis to
Essential References Not Discussed: Most of the works review know has been properly cited in the paper.
Other Strengths And Weaknesses: 1. For the reach-avoid case, the authors prove a regret bound on the order of $O(\sqrt{K})$ for K episodes, with high probability.
2. By extension, for the general LTL setting (using the product MDP trick), the same $O(\sqrt{K})$ scaling holds again, under certain assumptions such as known pmin and the ability to treat non-accepting states or MECs as “resets.”
3. They mention gridworld-type experiments showing that their approach converges faster than a purely PAC-based method from prior literature. While not a large-scale experiment, it demonstrates that the theoretical advantage—sublinear regret—can also manifest as faster finite-time progress in practice.
4. The biggest step forward is a proven finite-time, sublinear regret guarantee for LTL tasks in unknown MDPs, extending ideas from optimistic exploration to logic-based specifications.
5. Once they can identify the sets of accepting vs. rejecting MECs (via pmin and some exploration episodes), they unify a wide class of LTL formulas under the same approach.
6. A key assumption is that pmin (a positive lower bound on all nonzero transition probabilities) is known in advance. This is not always realistic.
Other Comments Or Suggestions: 1. It would be better to improve the writing for section 4.1. Each sub-section in 4.1 seems quite detached from each other.
Questions For Authors: 1. reviewer is curious in eq4 how the bound of plausible MDPs is chosen? And what is the intuition behind current MDPs' transition bound?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank you for the detailed and useful feedback! We plan to improve our paper taking your comments into account. Our response to your specific questions are summarized as follows.
**Discussion on the practicality of known lower bounds for transition probabilities:**
We agree with the reviewer that in a practice deriving $p_{min}$ might be challenging. However, all we need is to know a positive lower bound for the minimum transition probability, and not its exact value. Further, the assumption of knowing $p_{min}$ is strictly weaker than the other typical assumptions such as knowing the underlying connection graph of MDP, and there are already negative results in the literature regarding the consequences of not knowing $p_{min}$ for learning against infinite-horizon specifications. Consider a simple MDP with a state set $S = \set{s_{\text{init}}, G}$ and a singleton action set $A = \set{a}$, where the only outgoing transition from the initial state $s_{\text{init}}$ has transition probability $T(s_{\text{init}}, a, G) = \varepsilon$. It is easy to observe that, while the optimal value is one, selecting any $p_{min} > \varepsilon$ results in learning an MDP where the optimal value becomes zero. Hence, knowledge of $p_{min}$ is crucial for effectively learning in infinite-horizon tasks. In practice, domain-specific knowledge of the target system can be helpful in order to choose a sensible value for $p_{min}$.
**Writing of section 4.1:**
Section 4.1 is specifically dedicated to explaining various components of the main algorithm (Algorithm 1). In particular, the following components of Algorithm 1 are discussed in detail: (1) the application of Equation (4) for computing confidence intervals, which are then used to construct interval MDPs from the observed data; (2) the operation of our proposed Extended Value Iteration method (Algorithm 2); and (3) the use of Equation (9) to compute episode-specific deadlines. These explanations are provided in the respective subsections of Section 4.1. We appreciate the reviewer’s comment and will revise the writing in Section 4.1 to clarify the connections between these subsections at the outset.
**Further clarification for Equation (4):**
Equation (4) is used for computing confidence intervals used for constructing interval MDPs, and it is derived at earlier work (see Lemma 4.1). It provides a confidence bound for transitions for every state-action pair $(s,a)$, and is used to construct the interval MDPs.
In the final version, we will include Equation (4) in the body of Lemma 4.1, and also give a brief explanation regarding the terms within Equation (4).
**Experimental results:**
As explained in Section 5, model checking for general LTL specifications over finite MDPs reduces to a reach-avoid problem over the corresponding product MDP. Therefore, regardless of the specific LTL specification, the final step always involves solving a reach-avoid problem in the product space. In response to the reviewer’s concern, we conducted an additional experiment using the same gridworld example described in the Appendix, but with a new LTL specification: “visit $G$ infinitely often while avoiding the walls.” The performance of our method remained consistent with the results reported in Figures 3, 4, and 5. Accordingly, we plan to revise the manuscript to replace the current reach-avoid task with this LTL specification. We will also include the corresponding Deterministic Rabin Automaton (DRA) and the structure of the resulting product MDP in the appendix. Finally, we would like to emphasize that the primary contribution of this paper is the development of the first regret-free controller synthesis algorithm. The experiments are primarily intended to provide insight into various aspects of the approach, including empirical performance, the gap between practical and theoretical sample complexity, and the effect of different episode lengths.
Proposed changes based on comments of reviewer 3:
- Improve writing of Section 4.1
- Include a remark on challenges related to estimating $p_{min}$ in practice
- Replace the current reach-avoid task with a more complex LTL specification and report the results, DRA and product MDP | Summary: This paper tackles the problem of reinforcement learning (RL) for satisfying linear temporal logic (LTL) specifications in unknown environments modeled as Markov Decision Processes (MDPs). The authors propose what they claim is the first regret-free online RL algorithm for LTL objectives. The approach centers on a specialized RL algorithm for infinite-horizon reach-avoid tasks (LTL “until” formulas), which is then extended to general LTL specifications by reducing them to reach-avoid problems using automata-based techniques. A separate sub-algorithm is provided to learn the underlying state-transition graph (needed for the LTL product automaton) under the assumption of a known minimum transition probability. The main contributions include rigorous finite-episode performance guarantees – in particular, a proof that the algorithm’s regret (difference in satisfaction probability compared to an optimal policy) grows only sublinearly with episodes, achieving $O(\sqrt{K})$ regret over $K$ episodes. This translates to sharp high-confidence bounds on how close the learned controller is to optimal after a finite number of learning episodes. In contrast to prior methods that only guarantee eventual convergence, this work provides insight into transient performance during learning. Experimentally, the paper demonstrates the algorithm on a gridworld scenario with an LTL reach-avoid goal, showing that it quickly learns an optimal policy (regret per episode drops near zero) and significantly outperforms a recent PAC-learning baseline in terms of learning speed. Overall, the paper’s algorithmic contributions lie in combining model-based RL (optimistic exploration, episodic resets) with formal methods (automata translation of LTL) to yield the first online LTL controller synthesis method with provable regret guarantees.
Claims And Evidence: The key claims of the paper are generally well-supported by the content. The claim of being the “first regret-free online algorithm” for LTL specifications appears justified. All major claims (novelty of the approach, sublinear regret, reduction to reach-avoid, need for known minimum transition probability, improved transient performance over previous methods) are either mathematically proven or empirically demonstrated. We did not find over-claiming: for instance, the authors openly acknowledge assumptions like known minimum transition probability, which has been used in previous work for identifying MECs/AMECs.
Methods And Evaluation Criteria: The methodology is well-chosen for the problem setting. The authors build on established RL techniques for unknown MDPs (optimistic model-based exploration in an episodic framework) and tailor them to the LTL context. In each learning episode, their algorithm constructs an interval MDP using collected data and computes an optimistic policy for a reach-avoid objective (using dynamic programming over that model). Importantly, they introduce an episode-specific deadline $H_k$ that serves as a maximum horizon for that episode’s execution. This deadline mechanism, combined with a reset whenever the agent encounters a trapping state that would prevent reaching the goal, is a sensible methodological choice to handle non-communicating MDPs and ensure the agent can continue learning without getting “stuck”. How practical this "reset button" in reality could be discussed. The evaluation criteria used in the paper align well with the methodology and objectives. The authors emphasize regret as the primary performance metric, which directly measures how well the algorithm is doing over time relative to an optimal policy. This is appropriate since the whole point is to guarantee low regret (i.e., near-optimal behavior even during learning).
Theoretical Claims: The paper provides a series of theorems and lemmas to support its theoretical claims, and these appear to be both clear and plausible. The main theoretical result is that the proposed algorithm achieves sublinear regret. The authors give a proof sketch for this (Theorem 4.4) which outlines the key idea: classifying episodes as “fast” or “slow” and showing that slow (lengthy) episodes are rare, while fast episodes incur essentially no regret. This reasoning is intuitive and aligns with known techniques in regret analysis for episodic MDPs – by ensuring that long exploratory episodes (which might cause more suboptimal steps) don’t happen too often, the total regret can be bounded. The proof sketch references standard concentration bounds and optimistic planning arguments, suggesting the authors are leveraging established frameworks like UCRL2 but adapted to the reach-avoid setting.
The reduction from general LTL to reach-avoid via automata is supported by known results in formal methods – the paper essentially assumes one can obtain a deterministic Rabin automaton for the LTL formula and then construct a product MDP. The graph learning algorithm (Alg. 5) is given to handle unknown transitions; its correctness is stated in terms of sample complexity (Theorem A.2 in the appendix) guaranteeing that with enough samples, the learned graph matches the true MDP’s graph with high probability. This is a sensible approach: by knowing a lower bound $p_{\min}$, one can detect missing transitions by repeated exploration. The theoretical claim that full LTL is not PAC-learnable without such an assumption has been shown in prior work, justifying its existence.
Experimental Designs Or Analyses: The experimental evaluation, presented in the appendix (Appendix C), is sound and provides evidence that the algorithm works as intended. The authors test their approach on a gridworld environment with a reach-avoid LTL specification (reach a goal region G while avoiding a set of bad states B). The gridworld setup is appropriate – it’s a classic scenario to evaluate goal-reaching under uncertainty – and they introduce stochasticity by making movements succeed with 90% probability and fail (stay in place) with 10% probability. This ensures the problem is non-trivial (the agent must deal with uncertainty). They also treat collisions with walls as entering an absorbing bad state B, which effectively simulates an environment where hitting a wall ends the episode (a realistic “failure” condition). The experimental metrics are well-chosen to match the paper’s objectives.
Supplementary Material: The submission includes substantial supplementary material which add completeness to the work. All the proofs of the theoretical results are provided in detail, which is crucial for a paper of this nature.
Relation To Broader Scientific Literature: The paper’s contributions are novel in the context of prior work on RL for temporal logic objectives. No previous work has achieved a regret bound for general LTL specifications in unknown MDPs – this is explicitly noted by the authors and supported by the literature. Earlier approaches to LTL control learning fell into two broad categories: (a) Model-free or heuristic RL methods that ensured eventual convergence (with high discount factors or reward shaping) but offered no finite-sample guarantees, and (b) PAC-learning approaches that provided probabilistic guarantees on the final policy but not on the online performance. This work constitutes a natural extension of the (b) approaches by including a regret analysis.
Essential References Not Discussed: The paper’s reference list and related work discussion appear to cover the important literature in this area.
Other Strengths And Weaknesses: Strengths: This work is original and significant. It tackles a known challenging gap – learning controllers for complex temporal logic goals with measurable performance during learning – and provides a novel solution with strong guarantees. Another strength is the clarity of presentation: the paper is well-structured (with a clear breakdown of the problem into subproblems), and important assumptions and definitions are stated upfront.
Weaknesses: One weakness is the strong assumption of knowing a positive lower bound on transition probabilities ($p_{\min}$). While the authors make it clear this is needed for full generality (since without it, one cannot even PAC-learn LTL), it does raise the question of how one might obtain such a bound in practice. In very large or continuous systems, $p_{\min}$ could be extremely small or unknown. Another weakness is related to experimental validation scope. The paper demonstrates the approach on a relatively simple task (gridworld with an “until” specification). It would have strengthened the paper to see an example of a more complex LTL formula (for instance, one with an eventuality that requires the system to visit a region repeatedly, or a combination of reach-avoid tasks) to ensure the method scales to those cases. The current experiment essentially tests the core reach-avoid algorithm (Alg.1) but does not stress-test the full general LTL pipeline (Alg.4 + Alg.5) in a complex scenario.
Other Comments Or Suggestions: Appendix C, “our algorithcm”
"episode length vary” should be “episode lengths vary”
Another suggestion is to provide a bit more clarification on the use of the term “sharp bounds” in the abstract – perhaps in the introduction or conclusion, explicitly state that the regret bound is on the order of $\sqrt{K}$ (with logarithmic factors) and that this is comparable to known lower bounds in simpler settings.
Questions For Authors: 1. How does the proposed algorithm scale with respect to the size of the state space and the complexity of the LTL formula?
2. The approach requires $p_{\min}$ to be known. How realistic is this in typical applications, and what are the consequences if $p_{\min}$ is unknown? Can the authors elaborate on how one might choose or estimate $p_{\min}$ in practice?
3. In the experimental evaluation, did the authors implement the graph-learning algorithm (Alg. 5), or did they assume the transition graph was known in advance for the gridworld?
4. The experiments show a faster convergence compared to the ω-PAC method. Could the authors provide more detail on this comparison?
5. The algorithm sets an initial episode deadline $H_1$ and then adjusts it. How is $H_1$ chosen, and how robust is the algorithm to this choice?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for appreciating the depth and technical strength of our results. We plan to improve our paper taking your comments into account. Our response to your specific questions are summarized as follows.
**Computational complexity:**
The primary computational steps in Algorithm 1 involve two key tasks: (1) executing the EVI algorithm, and (2) calculating $H_k$. The computational complexity of these tasks, respectively, scales quadratically and cubically, with the size of the state space. As a result, the overall computational complexity of Algorithm 1 is cubic with respect to $|S^\times| = |S| \times |Q|$, where $S$ is the state space of the MDP, and $Q$ is the state space of the DRA that corresponds to the given LTL specification.
**Discussion on the practicality of known lower bounds for transition probabilities:**
We agree with the reviewer that in a practice deriving $p_{min}$ might be challenging. However, all we need is to know a positive lower bound for the minimum transition probability, and not its exact value. Further, the assumption of knowing $p_{min}$ is strictly weaker than the other typical assumptions such as knowing the underlying connection graph of MDP, and there are already negative results in the literature regarding the consequences of not knowing $p_{min}$ for learning against infinite-horizon specifications. Consider a simple MDP with a state set $S = \set{s_{\text{init}}, G}$ and a singleton action set $A = \set{a}$, where the only outgoing transition from the initial state $s_{\text{init}}$ has transition probability $T(s_{\text{init}}, a, G) = \varepsilon$. It is easy to observe that, while the optimal value is one, selecting any $p_{min} > \varepsilon$ results in learning an MDP where the optimal value becomes zero. Hence, knowledge of $p_{min}$ is crucial for effectively learning in infinite-horizon tasks. In practice, domain-specific knowledge of the target system can be helpful in order to choose a sensible value for $p_{min}$.
**Experimental results:**
- Clarification regarding the implementation: We implemented only Algorithm 1 to obtain the results presented in the Appendix, assuming that the underlying graph structure is known. This assumption is justified by the fact that, for a fixed system dynamics, Algorithm 5 needs to be executed only once to learn the corresponding graph with the desired confidence. The resulting graph can then be reused for verifying any LTL specification. We will ensure that this assumption and its justification are stated explicitly in the final version of the paper.
- Faster convergence compared to the $\omega$-PAC method: We believe that this is because our algorithm uses the intermediate confidence bounds, while the $\omega$-PAC algorithm waits until enough samples are collected, and only then starts updating its policy.
- Scalability against more complex LTL specifications: As explained in Section 5, model checking for general LTL specifications over finite MDPs reduces to a reach-avoid problem over the corresponding product MDP. Therefore, regardless of the specific LTL specification, the final step always involves solving a reach-avoid problem in the product space. In response to the reviewer’s concern, we conducted an additional experiment using the same gridworld example described in the Appendix, but with a new LTL specification: "visit $G$ infinitely often while avoiding the walls". The performance of our method remained consistent with the results reported in Figures 3, 4, and 5. Accordingly, we plan to revise the manuscript to replace the current reach-avoid task with this LTL specification. We will also include the corresponding Deterministic Rabin Automaton (DRA) and the structure of the resulting product MDP in the appendix. Finally, we would like to emphasize that the primary contribution of this paper is the development of the first regret-free controller synthesis algorithm. The experiments are primarily intended to provide insight into various aspects of the approach, including empirical performance, the gap between practical and theoretical sample complexity, and the effect of different episode lengths.
**Initialization for $H_1$:**
Actually, we compute $H_1$, rather than starting with a choice. This is because we first run EVI to get an optimistic policy $\tilde \pi_1$ and an optimistic MDP $\mathcal{\tilde M}_1$. A DTMC with transition probability matrix $\tilde{P}_1$ is induced by fixing $\tilde \pi_1$ over $\mathcal{\tilde M}_1$, and then we use Equation (10) to derive $\tilde{Q}_1$. Finally, we use $\tilde{Q}_1$ to compute $H_1$ by using Equation (9).
**Proposed changes based on comments of reviewer 2:**
- Include a remark on challenges related to estimating $p_{min}$ in practice
- Explicitly mention that the reported experimental results correspond to run of Algorithm 1
- Replace the current reach-avoid task with a more complex LTL specification and report the results, DRA and product MDP | Summary: This paper proposes a regret-free online RL algorithm for learning policies that satisfy infinite-horizon LTL specifications in unknown MDPs. The core contribution is an algorithm that, for reach-avoid specifications (a subclass of LTL), builds a sequence of optimistic policies using *interval* MDPs and extended value iteration, ensuring that the average regret—defined as the difference in satisfaction probabilities between the learned and optimal policies—converges to zero. The authors then extend this to general LTL specifications by transforming the original problem into a reach-avoid problem over a product MDP composed with a deterministic Rabin automaton, using an auxiliary algorithm to learn the graph structure of the unknown MDP given a known lower bound on transition probabilities. They provide theoretical regret bounds and claim sublinear regret in the number of episodes, supported by a regret decomposition analysis. Experimental results in the appendix in a gridworld domain are presented to suggest improved sample efficiency over a prior PAC-MDP approach.
Claims And Evidence: While the paper presents a complete pipeline and claims theoretical guarantees, the mathematical formulation and algorithmic descriptions are occasionally imprecise, and the overall presentation order may obscure key assumptions or derivations. Hence, the writing and proofs provided in support of the claims are not clear and convincing.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: - Lemma 4.1. (Tarbouriech et al., 2020) is unclear since:
- It is unclear what is the specific Lemma/Theorem from Tarbouriech et al. (2020) that is being restated here.
- $\mathbb{P}(\mathcal{E})$ is undefined (note that the authors generally use the notation $Pr$ to refer to probability distributions).
- The proofs of most of the Lemmas and Theorems use the results of Tarbouriech et al. (2020), but that means the authors must assume that the MDPs are SSP-communicating. However, this assumption is not stated in the paper (neither in *Problem 1* nor *Problem 2* statements). It is unclear what other specific assumptions are made but not stated.
Experimental Designs Or Analyses: N/A
Supplementary Material: No
Relation To Broader Scientific Literature: The paper builds on prior work in reinforcement learning with temporal logic specifications, particularly extending ideas from PAC-MDP and UCRL2 frameworks by aiming for regret bounds rather than asymptotic guarantees. It distinguishes itself from earlier approaches by handling non-communicating MDPs and providing better finite-time performance guarantees (regret of $O(K^{1/2})$) than the closest related prior work (regret of $O(K^{3/2})$).
Essential References Not Discussed: The paper extensively covers related works.
Other Strengths And Weaknesses: The paper provides a comprehensive number of algorithms and theoretical results. However, it is extremely unclear in its writing making it hard to follow and evaluate its correctness.
- The algorithms are not clearly explained. For example, at the start of Section 4.1 the authors mention "Alg. 1 shows our learning algorithm.". But Alg. 1 cannot be understood at that point since it references Alg. 2, Eq. 4, and Eq. 9 which only appear later (where Alg. 2 and Eq. 4 are also not clearly explained). Additionally, it is unclear what the notation #$\\{t < t_k : s_t = s, a_t = a\\}$ means (same for #$\\{t < t_k : s_t = s, a_t = a, s_{t+1}=s'\\}$). Is it a set of only one Boolean value (the result of $t < t_k$)?
- Alg. 2 and Alg. 3 are not clearly explained. In fact, Alg. 2 uses Alg. 3, but Alg. 3 is not even referenced in the text. It would have helped if the authors clearly explained their extended value iteration, and how exactly they obtain a policy that maximizes the probability of reaching G.
Finally, this makes even the main algorithm (Alg. 4) unclear since it uses Alg. 1, and makes the correctness of the corresponding main theorem (Theorem 5.1) hard to evaluate. Hence, while I think the problem this paper attempts to solve is very relevant, and the paper offers numerous interesting algorithms and theoretical results, its presentation is currently too unclear.
# Post Rebuttal
The authors rebuttal did help a bit clarify the assumptions they make in this paper, their definition of $\mathbb{P}(.)$ (how it differs from $Pr$), where Lemma 4.1 comes from, and the explanation for Equation (4). Unfortunately, I still have reservations regarding the clarity of the paper (listed below). However, I can see that the other reviewers feel positive about the paper, so it is possible that I missed something.
- It is still unclear how the authors can simply use Lemma 3 from Tarbouriech et al. (2020) if the authors are not assuming SSP-communicating MDPs. Perhaps I am misunderstanding the assumptions of that Lemma. Additionally, it is unclear how that Lemma is the same as Lemma 4.1 when:
- $\mathcal{E}$ from Lemma 4.1 is defined differently from $\mathcal{E}$ in Tarbouriech et al. Lemma 3. If one follows from the other, no explanation is given on how.
- For a given $\delta \in(0,1)$, the bound from Tarbouriech et al. Lemma 3 is $\mathbb{P}(\mathcal{E})\geq1-\frac{\delta}{3}$ but the one in Lemma 4.1 is $\mathbb{P}(\mathcal{E})\geq 1-\delta$.
- If the authors are not assuming SSP-communicating MDPs or the existence of a proper policy, then it seems like $\Lambda(s)$ and $\lambda^*(s)$ can be unbounded for some $s$, invalidating Lemma 4.2. For example, Consider a simple MDP with a state set $S = \set{s_{\text{init}}, s_1,s_2, G}$ and a singleton action set $A=\\{a\\}$. The transition probabilities are $T(s_{\text{init}}, a, G) = p_{min}$, $T(s_{\text{init}}, a, s_1) = 1-p_{min}$, $T(s_1, a, s_2) = 1-p_{min}$, and $T(s_2, a, s_1) = p_{min}$. Then $\Lambda(s)$ and $\lambda^*(s)$ are unbounded.
- The authors still did not clarify the notation #{.} in their rebuttal (they did not even confirm or denied the interpretation I gave), and in general they did not clarify my concerns with Algorithm 1. As I already highlighted in my review, I didn't find the presentation of Algorithm 1 nor the explanations given Section 4.1 entirely clear. Hence it did not help when they simply referred me back to Section 4.1 without an attempt to clarify at least some of those concerns (e.g. regarding how their EVI is able to find a policy that maximizes the probability of reaching G).
In general, I think the paper makes sense at a high level, and the specific algorithms are very interesting and do look like they work. However, given the focus of this paper theoretical guarantees, the impreciseness and potentially incomplete assumptions are problematic. Hence, I am maintaining my score for the moment but I am happy to update it if the other reviewers feel differently about these outstanding concerns.
Other Comments Or Suggestions: - No explanation is given for the right hand side of Equation 4 (not even an intuitive/brief one). E.g Why $8|S| log(2|A|k/3δ)$ in the numerator? Why $max (1,N_k(s, a))$ in the denominator? Why the square-root?
- It is unclear what is an optimistic MDP $\mathcal{\tilde M}\_k \in \mathbf{\mathcal{M}}\_k$ . Please define it.
- Remark 4.3. says "One may notice that the set B also includes every MEC whose intersection with G is empty.". How can this be true given that B is a set of states and a MEC is an MDP (from the definition in Sec 3)?
- Cite the definition of MDPs used in the preliminaries section, or explicitly mention how it is different from a typical definition (cite).
- cite maximal end components (MEC)
- Cite extended value iteration (EVI)
- Define and cite what is an Interval Markov Decision Processes
- Line 410 should use $T^\times : S^\times \times A^\times \times S^\times$ instead of $T^\times : S^\times$
Questions For Authors: Please refer to my weaknesses and comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank you for the detailed and useful feedback! We plan to improve our paper taking your comments into account. Our response to your specific questions are summarized as follows.
**Assumptions used in the paper:**
We do not assume the SSP-communicating property for MDPs. Instead, we **only** make a weaker assumption of knowing a non-zero lower bound over minimum transition probability $p_{min}$, which enables application of our method to the general non-communicating MDPs. To relax the communicating assumption in Tarbouriech et al. (2020), we leverage $p_{min}$ to compute $\Lambda(s)$, which represents an upper bound on the minimum expected time required to reach $G$ from state $s$ in the (artificial) MDP $\mathcal{M}'$, constructed by connecting $B$ to $𝑠_{𝑖𝑛𝑖𝑡}$. Note that $p_{min}$ can be used to compute the underlying graph to any desired accuracy, enabling us to check whether $G$ is reachable (which implies the boundedness of $\Lambda(s)$). These details are discussed in Lemma 4.2 and Remark 4.3. In particular, our results require **no** assumption other than knowing $p_{min}$. Also, it should be noted that assuming knowledge of $p_{min}$ is strictly weaker than the assumption of SSP-communication.
**Presentation of Algorithm 1:**
Regarding referencing other algorithms and equations, we would like to highlight that Section 4.1 is specifically dedicated to explaining various components of the main algorithm (Algorithm 1). In particular, the following components of Algorithm 1 are discussed in detail: (1) the application of Equation (4) for “computing confidence intervals”, which are then used to construct interval MDPs from the observed data; (2) the operation of our proposed “Extended Value Iteration” method (Algorithm 2); and (3) the use of Equation (9) to compute “episode-specific deadlines”. These explanations are provided in the respective subsections of Section 4.1. That said, we appreciate the reviewer’s comment and will, in the final version of the paper, provide additional intuitive explanations of our Extended Value Iteration (Algorithm 2), include a brief description of Algorithm 3, and define the notation \#{.}, which denotes set cardinality.
**Clarity of Lemma 4.1:**
In Lemma 4.1, the event $\mathcal{E}$ refers to the scenario where the actual MDP lies within the interval MDP computed during the $k^{th}$ episode of learning. The notation $\mathbb{P}(\mathcal{E})$ represents the probability that this event occurs. The notation $Pr_{s_{init}}^{\pi}[\varphi]$ is explicitly defined in Section 3 under the heading “Maximum Probability of Satisfaction”, and refers to the probability of satisfying a given LTL specification $\varphi$, starting from the initial state $s_{init}$ and following policy $\pi$. In the camera-ready version of our paper, we will ensure that the notation $\mathbb{P}(.)$ is clearly explained, replace instances of $Pr[.]$ by $\mathbb{P}(.)$, and we will explicitly reference the relevant lemma adapted from (Tarbouriech et al., 2020, Lemma 3).
**Comment on missing explanation for Equation (4):**
Equation (4) is used for computing confidence intervals necessary for constructing interval MDPs, and it is derived in earlier work (see Lemma 1). Specifically, the derivation relies on well-known probabilistic inequalities, and $ max(1, N_k(s,a))$ serves to prevent division by zero, where $N_k(s,a)$ represents the number of visits to the state-action pair $(s, a)$. In the final version, we will include Equation (4) within the body of Lemma 4.1 and provide a brief explanation of the terms in Equation (4).
**Proposed changes based on comments of reviewer 1:**
- Provide additional intuitive explanation of our EVI (Algorithm 2), and give a brief explanation of Algorithm 3
- Integrate Equation (4) into Lemma 4.1, and provide a brief explanation of the terms within Equation (4)
- Explain the notation $\mathbb{P}(.)$ under the notations section
- Define the notation \#{.}
- Provide citations for the definition of MDPs and interval MDPs (IMDPs), maximal end components (MECs), extended value iteration (EVI), and refer to the specific lemma from (Tarbouriech et al., 2020) for Lemma 4.1
- Define optimistic MDPs | null | null | null | null | null | null | null | null |
LIVS: A Pluralistic Alignment Dataset for Inclusive Public Spaces | Accept (poster) | Summary: The paper presents the Local Intersectional Visual Spaces (LIVS) dataset, a community-driven benchmark designed to align text-to-image (T2I) models with intersectional criteria for inclusive urban design. Through a two-year collaboration involving 30 community organizations, the authors iteratively refined 634 initial design concepts into six core criteria (Accessibility, Safety, Comfort, Invitingness, Inclusivity, Diversity) using participatory workshops and 37,710 pairwise comparisons. By applying Direct Preference Optimization (DPO) to fine-tune Stable Diffusion XL (SDXL), they demonstrate improved alignment with these criteria.
Claims And Evidence: Supported Claim: DPO enhances alignment for criteria with sufficient annotation support, as evidenced by the user study in Case Study I and Figures 6, 12–14.
Unsupported Claim: While the authors assert that their work proposes a pluralistic alignment framework for T2I models, this claim lacks justification. Since DPO's training signals remain confined to binary preference pairs and do not explicitly model intersectional interactions between criteria, no true multi-criteria framework is established. Notably, neither algorithmic adaptations nor multi-objective optimization strategies are introduced.
Methods And Evaluation Criteria: The participatory methodology for dataset construction (e.g., workshops, iterative concept refinement, pairwise comparisons) is clearly articulated and contextually appropriate for capturing community-driven priorities. However, the technical alignment approach relies entirely on off-the-shelf DPO without innovations addressing multi-criteria challenges. Evaluations include user studies and qualitative analyses, but standard quantitative metrics for T2I alignment (e.g., CLIP scores, FID) are notably absent.
Theoretical Claims: No theoretical claims or formal proofs are presented.
Experimental Designs Or Analyses: Experiments center on four user study-based case analyses: Case Study I demonstrates DPO's effectiveness for high-data criteria; identity-driven analyses (Cases II/IV) reveal preference variations across demographics; Case III underscores the critical role of prompt design in evaluation reliability. A reliance on qualitative outcomes persists, with quantitative metrics omitted.
Supplementary Material: Supplementary materials detail the LIVS dataset creation process, SDXL-DPO implementation specifics and more results.
Relation To Broader Scientific Literature: This work is related to T2I alignment methods relying on global metrics (ImageReward, HPS) and multi-criteria preference learning (MPS). It extends these by grounding multi-attribute annotations and local urban design contexts.
Essential References Not Discussed: None
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: The paper’s main contribution is its dataset construction, which is well explained and offers useful insights for future work. However, the claimed pluralistic alignment framework is unclear, as the DPO algorithm remains binary and only the annotations are multi-criteria—a concept already explored in prior works (e.g., ImageReward). Overall, this work is more of an excellent project than a novel research contribution. I am willing to raise my score if the authors can address my concerns.
Questions For Authors: Figure 1's caption references the inclusion of age, gender, race/ethnicity, and disability demographics, yet only age distributions are visually presented. Where are other demographic breakdowns (e.g., gender ratios) reported or illustrated?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We greatly appreciate the reviewer’s feedback. In response, we have clarified our methodological framing of pluralistic alignment, explicitly acknowledged the limitations regarding global metrics such as CLIP and FID, and revised Figure 1 for consistency and clarity.
---
### 1: The claimed pluralistic alignment lacks support, relying on binary DPO without modeling intersectionality.
**Response:**
We propose a pluralistic alignment framework, as our dataset and workflow explicitly incorporate multiple criteria—Accessibility, Safety, Comfort, Invitingness, Inclusivity, and Diversity—each annotated independently. While we apply DPO, our primary aim is to test its capacity to capture community-driven, intersecting needs. The core contribution of this work lies not only in the dataset itself but in the participatory framework through which it was created. Our originality lies in operationalizing pluralistic alignment: from co-developing multi-criteria definitions with communities, to collecting fine-grained preference data, to empirically fine-tuning a T2I model. We further demonstrate how DPO can be extended to reflect localized values. Models fine-tuned on LIVS and other datasets developed using this framework have potential applications in community consultations and urban design processes. We hope the reviewer recognizes that this approach meaningfully advances alignment research by grounding it in real-world civic contexts. Our human preference data offer greater relevance for intersectional, community-based alignment than generic image quality metrics. The high proportion of neutral judgments, in particular, underscores the complexity of socio-spatial values—dimensions that standard T2I evaluation metrics are ill-equipped to measure.
To further clarify this distinction, we have revised the relevant text in the Introduction section as follows.
**Revised text in Introduction:**
*“We propose a participatory data-collection framework that captures intersectional, multi-criteria feedback for T2I models in inclusive public-space contexts. While we refer to this as a *pluralistic alignment* approach to emphasize the local diversity of preferences, our method currently employs standard DPO with binary preference pairs, rather than a specialized multi-objective optimization algorithm. By integrating multiple locally defined criteria into preference annotations, we aim to expose both the potential and the limitations of a single-objective approach in accommodating intersectional needs.”*
---
### 2: No CLIP or FID; relies on user qualitative analysis
**Response:**
We intentionally foreground community-derived judgments over global image-similarity metrics, as our primary aim is to assess how well the generated images align with local, context-specific criteria. FID, measures similarity to a global real-image distribution and is not meaningful in our context. We also avoid CLIP-based metrics, as prior work ([1], [2]) shows weak correlation with human judgments. Given our focus on subtle, value-driven distinctions across communities, relying on CLIP risks missing the very nuances we aim to evaluate.
Nonetheless, we acknowledge that such metrics can provide useful insights into broader questions—such as identifying common features shared by inclusive spaces across different typologies.
**To reflect CLIP and FID limitations, we added this to the Limitations section:**
*“Our evaluation centers on human preference judgments rather than traditional metrics such as CLIP scores. While these metrics are useful for quantifying generative fidelity, they fall short in capturing nuanced, local, or intersectional considerations. ”*
---
### 3: Figure 1 problem
**Response:**
Revised Figure 1 for clarity and consistency.
---
### 4: More project than a novel research contribution.
**Response:**
We respectfully disagree. Our framework and dataset are novel on multiple levels: (i) they capture multi-criteria feedback from diverse communities, thereby reflecting nuanced, real-world norms; (ii) they empirically demonstrate how DPO performs on intersectional needs, exposing a key gap in current alignment methods; and (iii) they introduce a participatory data collection framework that systematically grounds alignment in heterogeneous civic contexts. Unlike ImageReward and other prior efforts that rely on homogeneous annotator pools, our pluralistic dataset and analysis illuminate both the potential and the limitations of single-objective alignment when values meaningfully differ across populations. This combination of empirical insights and community-based methodology advances alignment research beyond conventional quality metrics, underscoring its broader social implications.
---
**References:**
[1] Ku et.al. VIEScore: Towards Explainable Metrics for Conditional Image Synthesis Evaluation. ACL 2024
[2] Ku et.al. ImagenHub: Standardizing the evaluation of conditional image generation models. ICLR 2024 | Summary: This paper introduces a new dataset LIVS, which encodes community-generated plurastic preference data towards text-to-image for urban planning. This dataset is is built from data collected from 30 community organizations to develop a framework of 6 axes along which urban public space design can be evaluated. Based on this framework, the authors collect the dataset of 38k human preference annotations.
The training split of this data is used to perform DPO finetuning on Stable Diffusion XL, which is then tested on the validation split for analysis. The authors find that the trained model has a considerable win rate over the baseline but also that half of the matchups have a neutral outcome, which is presumed to illustrate the subjective and plural nature of the criteria.
Claims And Evidence: The authors claim that DPO taking into account multi-criteria feedback improves image generation in their considered space of urban planning. This claim is supported by their evidence (e.g. 70% win rate among non-neutral judgments). However, the extent of the claim is made weaker by the dominance of neutral judgments, accounting for more than half of the results. Given that collecting more training data to strengthen the claim may be costly due to the rigor involved, it might have been helpful to see a more nuanced breakdown using the existing training data: for example, by showing relative effects on different axes of evaluation when prioritizing those axes during DPO training.
The authors also claim that the significance of neutral judgments is that they highlight where "preferences are balanced or where further refinement is needed to accommodate complex intersectional needs". However, it is possible that a large proportion of neutral judgments also highlight axes of evaluation which may not be picked up by the participants comparing images. Particularly from the proportions displayed in Figure 5, as well as the description of late-joining participants in S4.2, it is possible that some of the axes (Diverse, Inclusive, Safe) may be too difficult or impossible for people to discern from concept art images.
Methods And Evaluation Criteria: The authors follow a meticulous and community-involved process to develop their framework of evaluation along 6 axes, and to collect training and testing data to illustrate the application of T2I in the urban planning space. Overall, this set of evaluations and analyses are well-defined and executed.
However, from their observations, the authors suggest that "less involvement in the knowledge-exchange process can lead to different or less pronounced alignment perceptions". For the purposes of expanding the scope of the study and data, it might have been helpful to expand upon definitions of the chosen concepts to allow more participants to offer their input and preference feedback with lower involvement. For instance, in addition to the short descriptions in S3.2, it would have been helpful to have compiled example images that illustrate the concepts being tested.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: Overall, the experimental designs and analyses appear well thought out. The authors explore multiple aspects of their results, including the effects of identity, intersectional interactions, and prompt compositions.
Supplementary Material: I skimmed the appendix, which includes detailed descriptions of their annotation tools and procedures, as well as examples images.
Relation To Broader Scientific Literature: The paper explores the role of T2I models in urban planning from a perspective of pluralistic values. While the paper does not contribute to the pluralistic theory itself, it uses it as a framework to develop a set of criteria with a human-centric method that may be useful in other scenarios as well. The work relates to a lot of prior work in finetuning T2I models for human preferences, but again, focuses on the local and community-centric nature of preferences, and uses them to present more convincing findings.
Essential References Not Discussed: None that I am aware of.
Other Strengths And Weaknesses: The paper presents the results of a very methodical and well-thought out approach to gathering real preference data from communities, targeting real issues deemed important by those communities. Overall, the paper is original and clear, though its significance is weakened at points due to the weakness of the overall results, which I address in other sections.
Other Comments Or Suggestions: Figure 1 is organized in an unintuitive way. The y axis shows age group, and it appears that all participants were assigned to one of four age groups, but these appear in no particular order. Why are the datapoints not sorted by age along the y axis?
Questions For Authors: The authors conclude that the reason for a large number of "neutral" annotations is the highly "subjective and plural nature" of determining alignment to people's criteria. However, to me, this appears underjustified (Q1 and 2).
1. At what point in the process, i.e. Workshops and Interviews, do you consider the relevance of the proposed axes of evaluation in concept art images? Is the determination of the 6 axes driven solely by holistic participant experiences and suggestions, or also by the plausibility of distinguishing those axes from an image?
2. Similarly, it is suggested that the 1100 neutral rankings during evaluation are due to pluralistic evaluation. Is this statement supported by other evidence, or is it possible that the models differ very little (in generation for particular prompts) or participants find it difficult to measure an image along particular axes?
3. From the example images and results, it appears that many of the generated images have only very subtle differences after DPO finetuning. Was the conditional guidance scale tuned during generation to ensure that annotators would be able to distinguish key differences between images from the same prompt?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their feedback. We clarified how criteria were defined, explained neutral judgments, revised Figure 1, and added detail on axis-specific outcomes and image generation settings.
---
### Question 1: Axes Relevance and Plausibility
**Response:**
It was both, since participants were looking at images during the focus groups. We revised our Criteria Consolidation section to clarify that the final six criteria emerged from community input on design and from probing whether each dimension could be assessed through images.
---
### Question 2: Neutral Judgments and Multi-Criteria Evaluation
**Response:**
We clarify that neutral judgments reflect both genuinely balanced preferences and difficulties in visually encoding certain criteria, especially Inclusivity and Diversity.
**New text in first paragraph in "Neutral Annotations as a Signal":**
*“Approximately half of the final evaluations were rated as neutral. While these outcomes may initially seem to indicate a lack of meaningful improvement, they could also stem from genuinely balanced preferences and participants’ difficulty in identifying visual cues for certain criteria (especially Inclusivity and Diversity). In several interviews, participants noted that subtle or symbolic elements did not always appear clearly. This indicates an opportunity to incorporate neutral signals explicitly into training and to explore methods that better visualize intangible attributes, such as inclusive design features, beyond purely aesthetic details.”*
---
### Question 3: Guidance Scale and Subtle Differences
**Response:**
Yes, we employed a moderate guidance scale during the image generation process. To ensure meaningful variation in outputs, we conducted pilot runs and fine-tuned hyperparameters such as seed, guidance scale, and steps. We also generated 20 images per prompt and used a greedy selection strategy, choosing the 4 most distinct images based on CLIP similarity scores, as detailed in Algorithm 1. This approach helped balance the risk of generating images with either overly subtle differences or excessively stylized divergences. We provide further clarification in Appendix (C.2. Image Generation).
---
### Comment 1: Figure 1 Organization
**Response:**
We have revised the figure (Reviewer iv23 also finds this problematic).
---
### Comment 2: More Nuanced Breakdown per Axis
**Response:**
We include additional discussion of axis-specific outcomes (see *New Paragraph below*), showing that some axes (Comfort, Invitingness) benefit more noticeably from DPO with more annotated examples.
**New Paragraph in "4.1 Additional Observations":**
*“We further analyzed alignment improvements on each criterion by correlating annotation counts with the DPO model’s win rate. The criteria that received more annotations (Comfort and Invitingness) exhibited stronger improvements, suggesting that denser feedback can refine criteria-specific features more effectively. In contrast, Inclusivity and Safety showed a higher proportion of neutral or mixed outcomes, possibly reflecting both fewer annotations and the inherent difficulty of visually conveying representational aspects through T2I alone.”*
**Please see the link below, which contains a figure on the Average Tendency Toward DPO by Criterion**
https://anonymous.4open.science/r/livs-6E96/average-tendency.png
---
**We hope these revisions address the reviewer’s concerns and enhance the clarity of our manuscript. Thank you for the valuable insights.** | Summary: The authors contribute LIVS, a benchmark for aligning text-to-image (T2I) models with respect to multiple criteria (Accessibility, Safety, Comfort, Invitingness, Inclusivity, and Diversity) in the context of urban public space design. The benchmark was developed via two-year participatory process with 30 community organizations in Montreal. The authors use DPO with 35,510 multi-criteria community preference annotations to align a Stable Diffusion XL model and find that: (1) the resultant generations can be better aligned with the preferences, (2) there remain a significant amount of neural ratings of the generations (possibly due to the complexity of modeling intersectional preferences), and (3) larger-scale alignment can be more effective. The authors also study the effect of prompt variation on community ratings of generations (observing that human-authored prompts are better at eliciting decisive preferences than synthetic prompts), and find that preferences vary across identities.
## Update after rebuttal
The authors provided a detailed response and suggested beneficial revisions based on my comments. I have maintained my (already high) score.
Claims And Evidence: - The claims are generally supported by clear and convincing evidence.
- Lines 76-77: The authors claim that their "approach applies multi-criteria preference learning," but they ultimately collapse the multi-criteria preference annotations into a single binary annotation via majority aggregation.
- Figure 3 does not provide clear evidence for the "comprehensiveness" of the prompt dataset (line 262).
Methods And Evaluation Criteria: - The authors facilitated an extensive participatory design process over two years with 30 community organizations, consisting of public education, 11 workshops, 34 interviews, and inclusive data collection. This methodology is excellent, as it positions community members as co-creators of LIVS, from criteria design to data annotation, and captures complex and diverse local preferences.
- The authors augment human-collected prompts with synthetic prompts generated using GPT-4o, but the synthetic prompts are not validated by humans (only validated automatically). The authors note in line 370 that the synthetic prompts likely lack "contextual specificity."
Theoretical Claims: The authors did not make any theoretical claims.
Experimental Designs Or Analyses: - To perform preference learning, the authors collapse the multi-criteria preference annotations into a single binary annotation via majority aggregation, which does not preserve differing intersectional preferences.
- The resultant generations from the aligned SDXL model are compared to generations from the baseline SDXL model on a held-out set of prompts, which is sound.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: - The authors thoroughly explore the relationship between their work and existing work on the alignment of generative models, intersectionality, visual generative modeling for urban spaces, and multi-criteria preference learning.
- The authors go beyond much prior work on global/universal alignment by capturing local multi-criteria preference annotations, specifically in the context of urban public space design.
- The authors go beyond the common conceptualization of Intersectionality as merely overlapping social groups [1] and discuss how overlapping forms of marginalizations affect people's preferences about, e.g., accessibility (Section 2.2).
- The authors build on the tradition of meeting community design objectives in urban planning.
- The paper is similar to prior work on multi-criteria preference learning, but does so by aligning SDXL with respect to multiple criteria (Accessibility, Safety, Comfort, Invitingness, Inclusivity, and Diversity) in the context of urban design.
- Some citations may not directly support the authors' claims, e.g., [2] in lines 115-119. The authors should double-check that all their parenthetical citations are directly relevant.
[1] https://dl.acm.org/doi/10.1145/3600211.3604705
[2] https://dl.acm.org/doi/10.1145/3613904.3642703
Essential References Not Discussed: I am not aware of any essential references that were not discussed.
Other Strengths And Weaknesses: Strengths:
- The authors focus on aligning models with local community preferences around inclusive urban planning, thereby advancing pluralistic alignment.
- The authors transparently document their ethics and inclusivity considerations, e.g., compensating community members, utilizing an inclusive and accessible data annotation interface.
- The paper is clearly written and well-organized.
- The authors offer numerous directions for future work, e.g., leveraging neutral annotations as a signal, disentangling ratings for overlapping criteria.
Weaknesses:
- The authors do not explicitly leverage neutral annotations or disagreements in annotations across criteria during preference learning.
Other Comments Or Suggestions: - Minor comment: The use of "democratizing" (line 43) requires further contextualization in the paper. In particular, the use of "democratizing" might be a bit misleading given that the paper does not discuss, e.g., democratic governance structures for T2I models in urban planning [1].
- The authors should expand on how their work relates to participatory action research.
[1] https://aclanthology.org/2024.emnlp-main.184/
Questions For Authors: - On average, how many criteria did a community member annotate per image pair?
- How may the definition of criteria like Inclusivity be refined to lead to more distinct preferences? Should the definition be more prescriptive or descriptive?
- In Figure 8, do the left and right images in a single pair come from the same or different models?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their detailed and constructive feedback. Below, we respond to each comment. Where revisions are needed, we provide the updated text.
---
### Comment 1: Multi-criteria preference learning but collapsing annotations, neutral annotations not leveraged; disagreements across criteria are collapsed
**Response:**
We acknowledge that our current method for DPO training reduces multi-criteria signals into a single reward label. While this dataset is inherently multi-criteria, this reduction reflects a pragmatic simplification for the initial phase of DPO training. However, this also underscores a broader limitation of DPO: it is not straightforward to perform multi-criteria alignment—particularly when preferences across criteria conflict or when alignment must be criteria-aware within the same model. We have clarified this in the revised text and emphasize that future work is needed to develop methods capable of capturing such partial, intersecting, or contradictory preferences in a more principled way.
**Revision in 2.1. Alignment of Generative Models:**
*“Although the LIVS dataset contains multi-criteria feedback, we initially collapse these signals into a single preference label for each pair during DPO. This step overlooks conflicting or nuanced assessments across different criteria. Future work is needed to explore approaches that account for intersections and disagreements without forcing a single binary label, thereby preserving the richness of multi-criteria preference data.”*
---
### Comment 2: Figure 3 does not clearly show "comprehensiveness" of prompts
**Response:**
We revised the text to clarify that the word cloud is a preliminary visualization of different concepts within prompts. We rely on Jensen–Shannon Divergence (JSD) scores and scenario-based coverage to demonstrate prompt diversity. The figure is meant only as an illustrative snapshot.
---
### Comment 3: Synthetic prompts not validated by humans
**Response:**
We acknowledge that synthetic prompts were primarily evaluated using automatic diversity checks (JSD). As noted in the limitations, this expands coverage but may lack the contextual specificity of human-authored prompts. Future work needs to incorporate human validation to improve relevance.
---
### Comment 4: Use of "democratizing" (line 43) requires more context
**Response:**
We removed the term “democratizing” and clarified that T2I tools aim to lower barriers to community participation in design. Thank you for the reference.
**Revised Sentence in Introduction:**
*“These developments can benefit communities by making design processes more accessible—enabling broader engagement among non-expert stakeholders in architecture, urban planning, and environmental visualization.”*
---
### Comment 5: Citation issue
**Response:**
Rectified.
---
### Comment 6: Participatory action research grounding
**Response:**
We added the following paragraph in the `Methodology: Building the LIVS Dataset` section.
**Revised Paragraph:**
*“Participatory Action Research (PAR). In line with the principles of PAR, our community-based approach centers on iterative, collaborative inquiry and reciprocal learning throughout the dataset development process (Israel et al., 1998; Cornish et al., 2023). By involving local organizations as active co-researchers, we ensured that the framing of inclusion, safety, and other design criteria emerged from lived experiences rather than external prescriptions. This iterative feedback loop aligns with PAR’s emphasis on collective problem-solving and empowerment, as participants guided each stage of data collection and model evaluation while gaining familiarity with T2I technology and its potential applications in urban contexts.”*
---
### Comment 7: Question—On average, how many criteria per image pair?
**Response:**
On average, each image pair received approximately 1.49 non-zero (decisive) annotations from community members.
---
### Comment 8: Question—Refining definitions like "Inclusivity" for more distinct preferences
**Response:**
This is a trade-off: while detailed definitions may yield clearer preferences, our prompts were prescriptive and annotations observational to avoid biasing participants. Now, with the full dataset, we plan to analyze each criterion by identifying subdimensions and associated objects for emerging patterns.
---
### Comment 9: Question—Figure 8: Do left and right images come from the same or different models?
**Response:**
Regarding Figure 9 (since Figure 8 pertains to prompt methods), both images were generated by the same SDXL model.
---
**We appreciate the suggestions, which helped clarify multi-criteria signals, prompt diversity, and neutral annotations. We believe the revisions address the reviewer’s concerns and strengthen the paper.**
**References**
1. Israel, B. A. et al. (1998). Annu. Rev. Public Health
2. Cornish, F. et al. (2023). Nat. Rev. Methods Primers
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed response and revisions based on my comments! I would like to maintain my (already high) score. | Summary: The authors of this paper collected a human preference dataset (called LIVS) of generated images about public spaces. The preference focuses on evaluating six metrics, including Accessibility, Safety, Comfort, Invitingness, Inclusivity, and Diversity. Then, they finetune a Stable Diffusion XL model using Direct Preference Optimization (DPO). The finetuned SDXL model's generated images got more preference than the original SDXL's images (32% vs 14%).
Claims And Evidence: - The authors claim that the LIVS dataset captures diverse, community generated dimensions of inclusive public space design. I think this claim is clearly supported by the data collection process, where communities participated in the workshops and condensed the evaluation metrics into six aspects.
- The authors showed the effectiveness of using the collected LIVS dataset (via DPO) to finetune SDXL towards human preference aligned with the six metrics. This claim is supported by the human evaluation experiment to compare the finetuned SDXL and the original one (Section 4.1).
- The authors suggested that their results show the influence of participant identities on model preferences and the difference of the generated images resulted from human-authored and AI-generated prompts. These claims are supported by Figure 7 and Figure 8, respetively.
Methods And Evaluation Criteria: The data collection is professional, where detailed instructions were given in a series of workshops and the annotators had sufficient understanding of the topic about public space design. The DPO is properly used to finetune SDXL with the collected preference data. Finally, it is correct to use human evaluation to check if the finetuned SDXL achieves better results than the original SDXL.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experimental analyses are mainly based on statistical analysis (Figures 4, 5, 7, 8), which show the distributions of ratings. This is the correct way to do the analysis.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The collected LIVS dataset would be useful in the community conerning public space design.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: I want to raise a fundamental question regarding the necessity of developing the LIVS dataset to improve the image generation models' capacity in generating images that align with the six aspects in designing public spaces. I think it might improve the images better by specifying a better, more detailed prompt. A simple prompting method is by appending the six criteria to the prompts. An example can be "a shopping mall with wide aisles, ramps, and accessible restrooms. It should follow these criteria: Accessibility, Safety, Comfort, Invitingness, Inclusivity, and Diversity." How does this strategy improve the generated images?
Other Comments Or Suggestions: No.
Questions For Authors: Why were only three randomly selected criteria from the total of six criteria shown in each annotation? Why not use all six criteria? Since the annotators have taken time to check the images, it would not take much more time to finish the evaluation on the remaining three criteria. Evaluating on all six criteria could results in more data with high efficiency.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the constructive feedback. We clarified the rationale behind using community-informed prompts over universal keywords, explained the three-criteria annotation design, and updated key sections for clarity.
---
### Comment 1: Necessity of the LIVS Dataset vs. Enhanced Prompting
**Response:**
We recognize that refined prompting strategies—for instance, appending keywords such as *accessibility*, *safety*, or *inclusivity*—can guide generative models toward more targeted outputs. Approximately half of the prompts used to generate images included at least one criterion (see Table 1). However, LIVS emphasizes that *lived experience* varies considerably across social identities and contexts. In many urban settings, local communities articulate inclusivity or accessibility in ways specific to their sociocultural histories. As demonstrated in prior research (e.g., Beebeejaun, 2017; McAndrews et al., 2023), relying solely on universal keywords can impose a fixed and potentially biased interpretation of inclusive space. By contrast, our dataset incorporates diverse local knowledge and community priorities, reducing the risk of reproducing a single design standard that may neglect intersectional needs (Crenshaw, 1997; Low, 2020).
**Table 1: Prompts with at least one of the six criteria vs. prompts without explicit criteria, and corresponding neutral response performance.**
| Prompt Type | % of Prompts | % Neutral Responses |
|------------------|--------------|----------------------|
| Without Criteria | 51.67% | 21.76% |
| With Criteria | 48.33% | 26.26% |
We adopted a localized approach without imposing a predefined notion of inclusive space on participants. Our objective was to maximize the diversity of both images and prompts, allowing for an emergent understanding of what *inclusive* or *diverse* space could mean in different contexts (Anttiroiko & De Jong, 2020; Madanipour, 2010). To our understanding, this design encourages community-driven insights rather than a one-size-fits-all approach to inclusivity.
**Revised Paragraph (in *Prompting and Early Feedback*):**
*“Although refined prompting techniques can shape generative outputs, universal keywords alone may overlook local sociocultural and historical contexts (Anttiroiko & De Jong, 2020; Beebeejaun, 2017; Talen, 2012). Our goal in creating the LIVS dataset was to integrate granular, community-generated perspectives on accessibility, safety, and inclusivity. By embedding localized knowledge, we reduce the likelihood of producing a uniform design standard that might disregard certain intersectional needs (Low, 2020; Madanipour, 2010; McAndrews et al., 2023).”*
---
### Comment 2: Annotating Only Three of the Six Criteria per Comparison
**Response:**
During our tutorial workshop, participants indicated that rating fewer or more than three criteria simultaneously was cognitively demanding and reduced their focus on each image. Including more criteria also gave a sense of reduced progress, especially since the initial annotation batches comprised around 1,000 comparisons, later reduced to 750. We also observed that displaying six rating elements constrained the interface, limiting visibility of the image pairs and making it harder to assess spatial details. As a result, we randomly assigned three criteria per annotation task. This approach balanced coverage and participant effort while preserving image clarity. We confirmed that all six criteria received substantial coverage across multiple batches.
**Revised Paragraph (in *Annotations and Evaluation*):**
*“To optimize data quality and minimize cognitive fatigue, we randomly presented three of the six criteria in each comparison. During pilot trials, participants found evaluating all six criteria difficult, which reduced their sense of progress and visual engagement. The multiple rating elements also constrained image size, making it harder to assess spatial details. Focusing on three criteria enabled more meaningful engagement. Over successive annotation batches, we ensured that all six criteria were robustly evaluated.”*
---
**We hope these clarifications and revisions address Reviewer's concerns. We appreciate their detailed comments, which have helped strengthen the methodological clarity and contextual framing of the paper.**
---
**References**
1. Anttiroiko, A.-V., & De Jong, M. (2020). *The Inclusive City*. Springer.
2. Beebeejaun, Y. (2017). Gender, urban space, and everyday life. *J. Urban Affairs, 39*(3).
3. Crenshaw, K. (1997). Demarginalizing intersectionality. In *Feminist Legal Theories*. Routledge.
4. Low, S. (2020). Social justice and public space. In *Companion to Public Space*. Routledge.
5. Madanipour, A. (2010). *Whose Public Space?* Routledge.
6. McAndrews, C. et al. (2023). Toward gender-inclusive streets. *J. Planning Lit., 38*(1).
7. Talen (2012). *Design for Diversity*. Routledge. | null | null | null | null | null | null |
Simultaneous Multi-Robot Motion Planning with Projected Diffusion Models | Accept (poster) | Summary: The paper proposes Simultaneous Multi-Robot Motion Planning with Projected Diffusion Models (SMD), a novel method for multi-robot motion planning (MRMP) that integrates constrained optimization into the sampling process of diffusion models. Although diffusion models have demonstrated promising capabilities in generating diverse and smooth robot trajectories, they often fail to satisfy essential constraints, including collision avoidance and kinematic feasibility. To address this, the authors introduce a constrained optimization approach embedded within the diffusion model's sampling process using an augmented Lagrangian method. This formulation efficiently projects generated trajectories into feasible spaces, ensuring compliance with both collision avoidance and kinematic constraints. Additionally, the authors provide a comprehensive new benchmark dataset to evaluate multi-robot motion planners across scenarios with varying obstacle densities and spatial complexities. Empirical results show that SMD significantly outperforms other baselines.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: No theoretical section is presented in the paper.
Experimental Designs Or Analyses: I find the experimental designs reasonable and sufficiently aligned with the paper’s objectives.
Supplementary Material: No
Relation To Broader Scientific Literature: This paper builds on prior score-based diffusion approaches and extends them by incorporating an augmented Lagrangian framework to handle multi-robot constraints, bridging a gap in the literature where most methods either rely on gradient-based cost penalties or post-hoc filtering for feasibility.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
The paper is well-written, and the proposed method is described clearly.
The combination of diffusion models with constrained optimization to ensure feasibility seems both novel and promising.
The comparisons against a strong baselines (including MMD) in the multi-robot motion planning setting help validate the method’s effectiveness.
Weaknesses:
It remains unclear how sensitive the method’s performance is to certain hyperparameters introduced by constrained optimization, and how difficult they are to tune in practice.
The paper lacks discussions about reproducibility and practical integration.
Other Comments Or Suggestions: While the core contribution is solid, additional details about computational overhead—particularly in comparison to MMD—would strengthen the paper.
Providing at least one reproducible example or making the code available would greatly help readers verify the claims and understand how easily the proposed SMD method can be integrated into existing robot planning systems or simulation environments.
Questions For Authors: How does SMD’s inference time scale with the number of robots (e.g., up to 100)? Do you have experimental evidence indicating whether it remains tractable for large-scale multi-robot scenarios?
Could you provide some results / explaintions on how senstive the performance of the proposed approach is to the additional hyperparameters introduced and how hard it is tune them?
In the early diffusion steps, when the trajectory is still highly noisy, wouldn't strongly enforcing constraints potentially lead to convergence towards unrealistic trajectories?
While the proposed benchmark is a valuable contribution, I have some concern that it might be biased toward your method’s strengths. Have you tested SMD on other existing benchmarks (e.g., those used in MMD) to confirm consistent performance improvements? Additionally, do you expect that SMD can handle more complex robotic systems (e.g., humanoid locomotion or higher-dimensional configuration spaces), rather than just 2D disk navigation?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the helpful review, in particular the acknowledgement of the **strong empirical performance** of our proposed SMD and the contribution of **a comprehensive benchmark** for MRMP. We provide below our answers to your insightful questions.
- **Q1: SMD’s inference time with more robots (e.g., up to 100) & experiments with large-scale scenarios?**
It would be amazing to succeed in such scenarios. However, these usually require much-simplified problems, including using a discretization of the underlying map in which multi-agent path finding (MAPF) formulation arises, and assumptions on fixed velocity and discretized environment
Please note that our proposed method scales to the **largest number of robots** in complex scenarios tested so far in this realistic setting, thus setting a new SOTA standard. Additionally, our newely proposed benchmark provides the most comprehensive robot scaling of any existing baselines. We are hopeful that our benchmark will be a useful contribution to the community.
We have also included additional inference times. Please refer to our response to Q3 from reviewer ZshS. Many thanks!
- **Q2: Senstivity analysis and tuning for the additional hyperparameters introduced**
Thank you for bringing up this point. During rebuttal, we have conducted an extensive senstivity analysis. We ask you to refer to our response to A3 from reviewer ZshS for more details.
The empirical observations strongly suggest that our method, being able to integrate constraints directly in the sampling phase of diffusion models, is very robust across a range of hyperparameters, thus reducing the need for meticulous tuning. This is a strength that we plan to discuss in the final version of the paper.
- **Q3: Concerns on generating unrealistic trajectories**
While the reviewer suggests that projecting early on in the diffusion process may "lead to convergence towards unrealistic trajectories," in fact, the opposite is consistently observed. First, consider a case where a single post-processing projection is used to correct the final sample $x_0$. If $x_0$ is far from the constraint set, the projection will alter the trajectories significantly, leading to a lower degree of realism. This is well documented by prior literature [1,2] and has motivated constraint imposition earlier on in the sampling process. By projecting earlier in the diffusion process, the following denoising steps will restore any reaslism that is lost by projecting. Instead, we converge to a feasible subdistribution of the training data.
Practically, the projection starting point could be tuned to balance the tradeoff between computational overhead and generation realism [2], but we defer this type of analysis to future research.
- **Q4: Performance evaluation on SMD's Benchmark & complex robotic systems**
Indeed, maps used in SMD's benchmarks contain fewer obstacles, under which both methods (ours and prior baselines) easily succeed. On more challenging maps, such as dense maps, our method demonstrates clear advantages.
The results on the original MMD benchmark can be found here:
https://drive.google.com/file/d/1fOCDaNoU6AP9-f5AvMuurvYSHsogwuNR/view?usp=drive_link
We would be happy to include them in the final version of the paper if the reviewer suggests so.
Regarding more complex scenarios, while this paper focuses on motion planning in environments with static obstacles, we agree that extending SMD to handle more complex systems (e.g., humanoid locomotion) is an exciting direction for future work. Indeed, our group is active in these directions. One possible extension is to incorporate human trajectory prediction into the projection mechanism, or to adopt a MPC framework to adapt to dynamic agents.
**Reviewer’s Additional Points**:
> **A1**:Reproducibility and practical integration
We agree and intend to release our code following the review cycle. It had previously been our intent to provide an anonymized repository with code examples for the rebuttal, but due to ICML's updated policy, we are only allowed to include figures, tables and explanations related to them in linked material. Our lab has a long tradition of sharing codes and associated github pages with execution instructions and tutorials.
As far as practical integration, our method is training-free and thus can be directly embedded into existing methods to improve performance. **This is also what allows us to generalize to unseen maps!**. The method is easy to use and requires minimal modification to existing pipelines.
---
Thank you for your time assessing our work! We appreciate your suggestions and will add the additional results that your review motivated to our subsequent draft. We would be grateful if you could consider increasing your score to reflect this. Many thanks!
[1] Christopher, Jacob K., et al. "Constrained synthesis with projected diffusion models."
[2] Yuan, Ye, et al. "Physdiff: Physics-guided human motion diffusion model." | Summary: The paper tackles constraint enforcement for trajectory generation with diffusion models in the context of multi-agent motion planning. Instead of encoding constraints as auxiliary energy terms, the paper proposes to project intermediate generations on to the collision-free manifold. The projection operator is tackled by dual ascent method so the formulation can be more tractable than solving the original constrained optimization problem. The method is shown to outperform standard diffusion model and variants with planning in-the-loop, in particular in complex problems with more agents and map layout entailing coordination.
Claims And Evidence: The central claim lies in using projection to enforce collision avoidance constraints is more amenable to generate solutions for complex multi-agent planning problems. This is validated by the results on dense and real-world maps in Figure 3.
Methods And Evaluation Criteria: The method follows literature-based formulation and dual ascent method for the effectiveness on solving constrained optimization. The reasoning looks solid although the insights about why the idea can bring about such effectiveness could be better addressed. The main issue on the method is that it seems heavily relying on the quadratic form of constraints that can only capture inter-distance between sphere-shaped robots. It is unclear whether other types of constraints can also be handled by the framework.
The evaluation is made on collision-free motion planning problems on maps with different levels of complexity and number of agents. The criteria on success rate makes sense.
Theoretical Claims: There is no theoretical result presented in the paper.
Experimental Designs Or Analyses: The experiment designs look sound to verify the acclaimed challenge of applying diffusion model to multi-agent motion planning and the effectiveness of projection based constraint enforcement. The analysis focuses on success rate of solving the problem and shows clear benefits of the proposed method in handling more complex setups.
Supplementary Material: The supplemental materials include a few files on the tested maps. No code or demonstrations are included as far as I can tell.
Relation To Broader Scientific Literature: The idea of leveraging alternating gradient descent to enforce constraints in denoising process seems applicable to broader works on embedding differential optimization in the learning loop. However, it is unclear whether the relaxation can work for non convex constraints other than a quadratic form which works for capturing the inter-agent collision avoidance but might be limited for general constraint enforcement.
Essential References Not Discussed: I am not aware of other essential references to be discussed.
Other Strengths And Weaknesses: The paper clarity can be improved as the method in beginning reads like a blend of sampling and gradient-based optimization. The details on training implementation is placed in the appendix so it was only clear to me at the end that the paper is about regressing solver's results. The clarity is also very demanding for the implementation of training. Algorithm 2 seems requires to differentiate though an optimization process and it is not clear from the paper whether the gradients are attained through unrolling the optimization process or adjoint methods.
The method seems to have some design space to explore, e.g. coefficients of constraint residual norms. An ablation study can better demonstrate the robustness of the method on the parameter choice.
Other Comments Or Suggestions: Line 164: "this allows it to from" missing a verb here?
Questions For Authors: 1. How can the framework be used to handle general multi-agent planning constraints beyond collision avoidance?
2. The problem seems not to cover anonymous agent planning. Can it be used on this category of problems?
3. What is the computational cost for the inference of diffusion model with embedded projection. Can it afford some replanning to close the loop?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your valuable feedback including acknowledging the **superior performance of our SMD in complex scenarios**. We provide below our answers to your valuable questions:
**Questions For Authors:**
- **Q1: How can the framework be used to handle general multi-agent planning constraints beyond collision avoidance?**
We agree that quadratic form of constraints used in our work usually captures inter-distance between sphere-shaped robots. Such a formulation is also **widely adopted by existing methods** (e.g., the previous SOTA, MPD and MMD used in our experiments) and can be found in practical environments [1]. If extended to other robot shapes like rectangles, our framework still works but with more complex constraints. A simple alternative is to use the minimum bounding sphere, or multiple spheres to approximate the irregular shapes.
We would like to clarify we do not *only* consider inter-distance constraints, but also **ensure the kinematical constraints (e.g., velocity limits)** in our paper. Additionally, SMD can handle other constraints such as acceleration and smoothness constraints easily by adding these to the constraint set. This could be a meaningful future direction. We will further elaborate in the final version of the paper.
- **Q2: The problem seems not to cover anonymous agent planning. Can it be used on this category of problems?**
Provided that anonymous agent planning is, in fact, a less constrained problem than MRMP, our method can be employed without changes if we preassign goals to agents. For better performance, we can modify the constraints governing the initial and final states of the agents.
- **Q3: What is the computational cost for the inference of diffusion model with embedded projection. Can it afford some replanning to close the loop?**
With a tolerable increase in runtime, our method achieved significant performance improvement over the previously SOTA methods! The detailed comparison is available at this link: https://drive.google.com/file/d/10AnaJkw5Sva8qdNtXbexmNst80pKKjnF/view?usp=drive_link. Our running time can be further optimized using multiple techniques, such as parallelism and learning to optimize methods.
Our method can be easily adapted to support replanning. In fact, this is our current focus. To do so, we adjust the input to incorporate the existing trajectories and perform local updates according to the changed conditions. This approach also significantly reduces computational overhead!
**Reviewer’s Additional Points**:
> **A1**: The reasoning behind the effectiveness of our method, and whether it generalizes beyond quadratic inter-distance constraints
For general constraints, please refer to our response to Q1 for details.
For theoretical and empirical analysis for the effectiveness of our SMD, please refer to our response to Q1 from Reviewer 7Hco.
> **A2**: Clarifying our sampling process
We're happy to clarify this, as it seems there are a few key misunderstandings of our work. First, there seems to be a misunderstanding regarding our approach, which is not merely a "blend of sampling and gradient-based optimization".
The gradients are computed based on the constraint residuals iteratively, which is a common practice in the *dual ascent method* in constrained optimization. Specifically, our approach leverages an optimization solver to project the infeasible trajectories — generated during the diffusion sampling process (from noise to trajectory) — onto the feasible region. This allows us to achieve SOTA performance.
Second, our paper's contribution is centered on extending the *sampling process* and is consequentially applied at *inference time only*. We defer details about training to the appendix because this is not where our work is centered. This aspect however, is important: **it is what allow us to generalize beyond training distribution and handle maps, even if they were never seen before**.
We will be happy to include the training details in the main text and provide a more detailed description of Algorithm 2 in the final version.
> **A3**: Coefficients of constraint residual norms
During rebuttal, we evaluated the convergence performance with 6 different coefficients for the constraint residual norms. The results are available at: https://drive.google.com/file/d/1jjlOs9GEYd2qE4X6OLd4wjEoR3PVkDwo/view?usp=drive_link
Importantly, there is no change w.r.t. the paper's conclusions.
---
We appreciate your efforts and insightful feedback! We believe our response has addressed each of your questions but would be happy to provide more details if requested. As the points covered in your review are primarily requests for clarifiying, we would be grateful if you could consider increasing your score to reflect this. Many thanks!
[1] Clearpath Robotics. *TurtleBot 4*. https://clearpathrobotics.com/turtlebot-4/
[2] Rockafellar, R. T. Augmented Lagrange multiplier functions and duality in nonconvex programming. | Summary: This paper proposes a new method for tackling the constraint satisfaction challenge in Multi-Robot Motion Planning (MRMP). The paper highlights challenges in existing methods, such as learning-based approaches, that struggle with obeying hard constraints. The proposed method, SMD, addresses these issues by incorporating constrained optimization into diffusion models. To handle nonconvex constraints efficiently, SMD employs an augmented Lagrangian method. This paper also proposes a MRMP benchmark with varied scenarios. SMD outperforms state-of-the-art MRMP methods in complex multi-robot settings.
Claims And Evidence: 1. The submission claims that SMD maintains feasibility as robot/obstacle density increases, however, MRMP complexity grows combinatorially with robot count.
2. The main contribution—integrating constrained optimization into diffusion via projections—appears closely aligned with Christopher et al. (2024). The primary adaptation here is applying this framework to MRMP and replacing the solver with an augmented Lagrangian method.
Methods And Evaluation Criteria: Yes
Theoretical Claims: No proofs.
Experimental Designs Or Analyses: Yes
Supplementary Material: The supplementary materials are .pkl files which contain benchmark instances.
Relation To Broader Scientific Literature: Generative diffusion models, Multi-Robot Motion Planning
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. The paper demonstrates the effectiveness of the proposed method.
2. The paper introduces a comprehensive benchmark tailored to MRMP.
Weaknesses:
The main contributions closely follow Christopher et al. (2024), with the main adaptations being its application to MRMP and the use of an augmented Lagrangian solver.
Other Comments Or Suggestions: It would be helpful if the authors could clarify any additional novelty/contributions.
Questions For Authors: Differentiation from Christopher et al. (2024)
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank Reviewer 9rTn for the insightful feedback including acknowledging the **effectiveness** of our proposed SMD and **comprehensive benchmark** for evaluating MRMP. We provide below our answers to your valuable questions:
- **Differentiation from Christopher et al. (2024)**
Indeed, our work draws inspiration from Christopher et al. (2024), but our contribution is far from being an application of the such framework. It is a significant extension specifically tailored to MRMP.
Our first key contribution is a diffusion-based method explicitly designed to overcome the challenge of ensuring trajectory feasibility in MRMP. Our SMD can consistently **generate feasible trajectories in complex MRMP scenarios where existing state-of-the-art methods fail**.
Furthermore, our approach extends projected diffusion models to MRMP by introducing **two key innovations beyond Christopher et al. (2024)**:
1. We propose a relaxation of the MRMP nonconvex constraints using an Augmented Lagrangian method, transforming the problem into a convex formulation. This significantly enhances projection efficiency. In contrast, Christopher et al. (2024)'s method **faces substantial difficulties** when solving even relatively simple MRMP instances even with 3 robots due to the complexity of nonconvex projections, and thus it cannot be applicable in practice.
2. As we shown in lines 208–219 in our paper, SMD ensures the outputs generated by diffusion models can satisfy convex constraints. For a more detailed theoretical analysis, we also refer the reviewer to our response to Comment 2 from Reviewer 7Hco.
Additionally, we contribute a **new benchmark** for evaluating MRMP methods, which has been valued by other reviewers and which we believe, will benefit this community. We will be more explicit about our contribution in the final version of the paper.
**Reviewer’s Additional Points**:
> The submission claims that SMD maintains feasibility as robot/obstacle density increases, however, MRMP complexity grows combinatorially with robot count
We agree that MRMP is highly challenging, especially in complex environments. Recent advances in MRMP exploit diffusion models to generate diverse solutions, but existing methods fail to satisfy non-collision, which is key, in complex environments. Such issues become more pronounced as robot/obstacle density increases. As shown in our experiments, the previous state-of-the-art methods **succeeds only in empty environments with 3 robots**, yet performance **significantly degrades to a 27.2% success rate with 9 robots and 20 obstacles**.
Unlike other methods whose success rates rapidly decline as robot and obstacle numbers grow, **SMD maintains feasibility in scenarios with increased robot and obstacle counts **(e.g., dense maps with 9 robots and 20 obstacles). Specifically, SMD is the only known method that **provides feasible solutions for the largest number of robots** in complex environments. Even in the most challenging dense maps, where it still maintains a near-perfect success rate.
As briefly mentioned above, to mitigate the computational complexity brought by the large number of obstacles and robots, we develop an Augmented Lagrangian-based projection, which **reformulates nonconvex MRMP into a convex problem**. This significantly enhances projection efficiency and make using projection-based methods in MRMP possible, without affecting its success rate.
Thank you for your points. We will further emphasize the significance of our results in the revised manuscript to help readers more directly appreciate our results.
---
We would like to sincerely thank you for your insightful feedback, which is valuable to improve our manuscript. We hope our responses have addressed your concerns and we would be grateful if you could consider increasing your score to reflect this. Many thanks!
---
Rebuttal Comment 1.1:
Comment: I thank the authors for clarifying the contribution. However, how can the satisfaction of the constraints be guaranteed theoretically? Due to the decentralized nature of multi-agent systems, I hope the authors elaborate on the applicability of SMD.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank reviewer 9rTn for going through our response.
First, let us clarify that our method, like many existing approaches to Multi-Robot Motion Planning, including its discrete counterpart (multi-agent path finding [4] ), is designed for a **centralized setting**, where a central planner coordinates all robots jointly. This is the standard assumption in prior work [1–3], and our approach follows this established line of research. This is evident from program (1) as well as the experimental setting in our paper. We also want to emphasize that our paper does not mentions the word "decentralized".
1. For **constraints feasibility guarantees**:
As explained in lines 208–219 of our paper, the derived projection operator satisfies **convex constraint feasibility guarantees**. The detailed theorem (the complete proof is in [5]) is:
*Let $\mathcal{P}\_\Omega$ be a projection onto convex set $\Omega$, $\mathbf{x}\_{t}^{i}$ be the sample at time step $t$ and iteration $i$, and $Error$ be the distance between $\mathbf{x}\_{t}^{i}$ and its nearest feasible point. Assume $\nabla\_{\mathbf{x}\_{t}} \log p(\mathbf{x}\_{t})$ is convex. For any $i \geq I$, we have:*
$$
\mathbb{E} \left[ \textit{Error}(\mathcal{U}(\mathbf{x}\_{t}^{i}), \Omega) \right] \geq \mathbb{E} \left[ \textit{Error}(\mathcal{U}(\mathcal{P}\_{\Omega}(\mathbf{x}\_{t}^{i})), \Omega) \right]
$$
*where $\mathcal{U} (\cdot)$ denotes a single update step for the sampling process.*
Although MRMP is inherently nonconvex, which prevents a direct application of this theorem, our Augmented Lagrangian-based projection reformulates MRMP into a convex problem, allowing generated trajectories from our SMD to **satisfy this relaxed version theoretically**. We handle the remaining nonconvex constraints via a dual ascent method, providing a clear stopping criterion and ensuring **constraint violations remain below the predetermined threshold**.
To the best of our knowledge, this is the first work offering these guarantees in diffusion-based trajectory planning. We will make sure to further emphasize this message and its theoretical justification in the revised manuscript.
2. The question of **decentralized multi-agent systems** is however intriguing and our method can be extended to the decentralized settings with minimal modifications. For example, we can consider a setting where each robot knows its own goal and has access to a local environmental information within a limited sensing range. Our method can be **directly applied** to generate a collision-free trajectories that approaches the goal within this local region and run SMD for each robot iteratively. It is challenging to provide theoretical guarantees for the whole problem but our method would still ensure **constraint satisfaction** and **significantly improve efficiency** due to the reduced dimensionality of the problems. This is an exciting direction for future work!
---
Thank you again for the review and suggestions. We hope that all of your questions have been addressed, and would be grateful if this could be better reflected in your final evaluation of our work. Thank you!
[1] Shaoul, Yorai, et al. "Multi-robot motion planning with diffusion models."
[2] Peasgood, Mike, et al. "A complete and scalable strategy for coordinating multiple robots within roadmaps."
[3] van Den Berg, Jur, et al. "Centralized path planning for multiple robots: Optimal decoupling into sequential plans."
[4] https://mapf.info
[5] Christopher, Jacob K, et al. "Constrained synthesis with projected diffusion models." | Summary: This paper introduces Simultaneous MRMP Diffusion (SMD), a novel method for enforcing critical constraints, such as collision avoidance and kinematic feasibility, in Multi-Robot Motion Planning (MRMP). SMD integrates constrained optimization into the diffusion process to generate collision-free, kinematically feasible trajectories, thereby embedding these constraints directly within the trajectory generation pipeline. A Lagrangian-dual based approach is employed to achieve this integration. Additionally, this work presents the first benchmark for MRMP evaluation, featuring complex input maps and diverse scenarios. Experimental results demonstrate that SMD outperforms both classical and learning-based motion planners, achieving higher success rates and greater efficiency in complex multi-robot environments.
Claims And Evidence: - This paper claims that diffusion processes integrated with constrained optimization helps produce collision-free, kinematically feasible trajectories but analysis on these aspects are missing from the experiments section.
- Theoretical justifications for projecting the diffusion process is unclear which leads to confusion and weakens the argument for using this particular method.
Methods And Evaluation Criteria: - Comparison candidates seems to be well chosen including state-of-the art methods which helps validate the results of the paper
- The random maps designed for MRMP experiments are well chosen which covers many scenarios and tests the ability of each planner to a high degree.
Theoretical Claims: - How the equations constrains each robot's trajectory is rather unclear and requires further explanation.
- In section 4.2 the process of the inequality being rewritten as equalities are missing which makes it harder to understand and appreciate.
Experimental Designs Or Analyses: - The experiments cover various scenarios including randomly generated and structured real-world-inspired maps.
- Random maps include environments with increasing difficulty. Basic maps introduce multiple obstacles which requires navigating through narrow corridors. Dense maps contain many obstacles significantly restricting movement. The various difficulties help test the planning algorithms to their limit.
- Practical maps include corridors, warehouse storage layouts with tight aisles, rooms connected with doors. These maps are well designed to test global coordination.
Supplementary Material: - This paper provides a .pkl file with a simple README text file on how to use the pkl files. Visualizations using the .pkl files should be submitted instead.
Relation To Broader Scientific Literature: - This paper proposes to constrain the diffusion process to avoid collisions and satisfy kinematic feasibility. Compared to previous works, a novel constrained optimization process is integrated into the diffusion process.
- Furthermore, this paper proposes a method for evaluating Multi-Robot Motion planning (MRMP) which can be used for future works.
Essential References Not Discussed: All necessary references are included in the paper. No further recommendations required.
Other Strengths And Weaknesses: - The proposed method achieves state-of-the-art results for MRMP.
- Rejection sampling or post-processing is not required for the proposed method.
- Proposing a new evaluation method is a meaningful contribution to the research community.
- Theoretical justifications lacks clarity and would benefit from further explanations.
- Figure 1's overview could be improved to clarify the projection operation.
Other Comments Or Suggestions: - On the last sentence in page 3, there is a typo: This allows it to from ~.
Questions For Authors: - Does projection actually help guarantee collision avoidance and kinematic feasibility?
- How does Simultaneous MRMP Diffusion perform on more complex plans where the trajectories are more complex?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for the helpful comments, in particular the acknowledgement of the **strong empirical performance** of our proposed SMD and **a novel benchmark** for MRMP. We provide below our answers to your constructive questions.
- **Q1: Does projection actually help guarantee collision avoidance and kinematic feasibility?**
From the **theoretical perspective**:
Firstly, In lines 208–219, we demonstrate that the derived projeciton operator satisfies both the **convergence and convex constraint feasibility guarantees**. Although MRMP is inherently nonconvex, our Augmented Lagrangian-based projection reformulates it into a convex problem, allowing generated trajectories from our SMD to **satisfy relaxed MRMP constraints theoretically**. We address remaining nonconvex constraints via a dual ascent method, providing a clear stopping criterion and ensuring **constraint violations less than a predetermined threshold**. To the best of our knowledge, this is the first work offering these guarantees in diffusion-based trajectory planning.
Next, if you ask *why project throughout the diffusion process?* The shortcomings of post-processing methods are well documented within the literature: It is shown to substantially degrade sample quality ([1] highlighs that samples are often too "implausible to be corrected... [and] may be pushed away from the data distribution.").
From the **empirical perspective**:
We do provide this analysis in our experiments. Performance is measured by success rate: **the percentage of collision-free, kinematically feasible trajectories in test cases**. SMD consistently achieves the highest success rate, significantly outperforming other diffusion-based approaches. Specifically, the **key difference between SMD and MPD (a baseline method in our experiments) is integrating constrained optimization into the diffusion process**. We will further clarify this aspect in the revised version providing a numerical summary in the introduction.
We will be happy to include a more formal statement of theoretical analysis in the final version.
- **Q2: How does Simultaneous MRMP Diffusion perform on more complex plans where the trajectories are more complex?**
We have evaluated our method in scenarios **significantly more challenging than those explored in previous studies**. Compared to MPD, we extend our experiments to multi-robot systems; compared to MMD (the previous SOTA appraoch, which was deposited on ArXiv only 3 months before this submission), we increase both the number and density of obstacles. **In fact, our paper even proposes a new benchmark that provides the highest degree of scaling within Multi-Robot Motion Planning to date.** Our method consistently achieves superior performance under these complex conditions. We agree that further investigation into more complicated scenarios, such as 3D environments, would be valuable; This is an important direction for future work.
**Reviewer’s Additional Points**:
> **A1**: Feasibility analysis in experiments section & Theoretical justifications for projecting the diffusion process
Please refer to our response to Q1 for details.
> **A2**: The process and effectiveness of reformulating inequality constraints into equality ones
We take a general inequality constraints as an example:
$$
h(x)\geq b,
$$
where $x$ is the decision variable and $b$ is a parameter. Directly handling Eq (1) with Augmented Lagrangian methods are complicated because multipliers for inequality constraints should be larger than 0, which introduces extra decision logic.
Instead, equality constraints can lead better convergence properties and simplify multiplier updates:
$$
\boldsymbol{\nu}^{k+1}=\boldsymbol{\nu}^{k}+\alpha^k\boldsymbol{h}(x^k)
$$
where $\boldsymbol{\nu}$ represents the multiplier and $\alpha$ is the step size.
To transform inequalities into equalities, we introduce non-negative auxiliary variables $s$:
$$
h(x)-b-s=0.
$$
The presence of non-negative variable $s$ can ensure Eq. (3) is equivalent to Eq. (1):
- If $h(x)\geq b$ , then $s=h(x)-b\geq0$ makes the equality hold.
- If $h(x)-b-s=0$ and $s\geq0$, then $h(x)-b=s\geq0$.
We will provide a more detailed description in the revised paper.
> **A3**: Visualizations for the Benchmark
We will include linked a GitHub page with visualizations in the final version: https://drive.google.com/drive/folders/1ZdfNmA9BfIdshIbRN3AmAcyvXakhrhkr?usp=drive_link
> **A4**: Figure 1’s overview
A new figure is here: https://drive.google.com/file/d/1W8tuHwVLBV-2zZ9It0pLIdny1ZHchoxF/view?usp=drive_link
Could you let us know if you have further suggestions?
---
We want to thank the reviewer again for their valuable feedback. We believe that our response has addressed each of your comments but are happy to provide additional details if requested. We would be grateful if you could consider increasing your score to reflect this. Many thanks!
[1] Yuan et al. "Physdiff: Physics-guided human motion diffusion model."
---
Rebuttal Comment 1.1:
Comment: The authors provided sincere and well-reasoned responses to the reviewer’s questions, supported by both theoretical explanations and experimental evidence. In particular, they adequately addressed feedback regarding the convergence and constraint satisfaction of the projection method, superior performance in complex scenarios, the transformation of mathematical constraints, and improvements to visual materials. They also clearly outlined their revision plans. However, it is somewhat regrettable that the theoretical justification for the projection and quantitative details on the constraint violation tolerance were not directly included in the main paper. I hope all of the authors' responses will be thoroughly reflected in the revised manuscript.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer 7Hco for the encouraging feedback! Of course, we will make sure to incorporate our responses into the final version, including the formal theoretical justification of the projection method and the quantitative details on constraint violation tolerance. Indeed, we have already modified the paper on our end.
If there are no further points of clarification, we would be grateful if you could consider further championing this work to reflect the improvements and clarifications we have provided. Thank you! | null | null | null | null | null | null |
Off-Policy Evaluation under Nonignorable Missing Data | Accept (poster) | Summary: The authors study and propose OPE for RL under monotone MNAR missing.
Specifically, they construct an IPW-based correction of value-based OPE and show that, unlike an uncorrected method, the proposed method is unbiased with MNAR missing process under the existence of a shadow variable.
They also conducted synthetic/real/semi-real numerical experiments to verify the effectiveness of the proposed method.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Partly yes.
Experimental Designs Or Analyses: Yes.
Supplementary Material: Partly yes. On the assumptions, selection of shadow variable, (a part of) the proof, and the experiment details.
Relation To Broader Scientific Literature: It provides a solution to a practical problem related to missing values that OPE methods will be faced with.
Essential References Not Discussed: None that I am aware of.
Other Strengths And Weaknesses: It is a solid contribution to the OPE literature and deserves to be accepted, as far as I can tell.
One thing I have noticed is that the Assumption A.1 is a bit unorganized with mixed levels of details. Can you factor out the details in (a), (b) and (e)?
Other Comments Or Suggestions: - L110: $p:S\times A\times S\to [0,1]$ only makes sense with discrete state space. Need some update.
- Please provide the definitions of B-spline and wavelet for the completeness.
Questions For Authors: It seems Assuption A.1 (d) (i) poses a concentrability condition on the feature map $\Phi_L$,
but how easy/difficult is it to satisfy this condition, especially if $\Phi_L$ is B-spline or wavelet?
Since $\Phi_L$ is fixed to one of these two, can you translate the condition in terms of the behavior distribution, e.g., to the boundedness of $\mu$ from below?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your thoughtful questions and the time you spent reviewing our paper. We really appreciate your insights and are happy to discuss any further ideas or questions you may have.
**Regarding Assumptions (a), (b), and (e):**
Below is a more detailed explanation of what each assumption means and how it is used in the proof. We hope this will help improve the clarity of the assumptions, and we will incorporate these explanations in the final version of our paper.
* Assumption (a):
We assume smoothness of the transition kernel $\mathcal{P}$. Specifically, when $0 < p \leq 1$, $\lfloor p \rfloor = 0$, and the condition becomes equivalent to assuming $h$ satisfies $\sup_{x, y} \frac{|h(x) - h(y)|}{\\|x - y\\|_2^p} \leq c$, which is a form of Hölder continuity. Under this assumption, it can be shown that there exists a constant $c' > 0$ such that $Q(\pi; \cdot, a) \in \Lambda(p, c')$ for any policy $\pi$ and $a \in \mathcal{A}$. This ensures that the $Q$-function has bounded derivatives up to order $\lfloor p \rfloor$, which is critical when deriving inference for the value function.
* Assumption (b):
This assumption is more of a claim or explanation rather than a strict assumption. Here we consider two types of basis functions, which are commonly used sieve basis functions. These are standard choices for such problems and serve to simplify the analysis while ensuring general applicability.
* Assumption (e): Here, $L$ controls the smoothness of the basis function, which in turn determines how closely the linear sieve basis function can approximate the true function. This assumption is used to ensure the $Q$ function is well approximated. In the proof of asymptotic normality, we rely on this condition on $L$ to establish that $\sup_{s \in \mathcal{S}, a \in \mathcal{A}} |Q(\pi; s, a) - \Phi_L^\top(x) \beta^*_{\pi, a}| = O(L^{-p/d})$, which guarantees the consistency and asymptotic behavior of $\hat{\beta}$ and the value estimates.
**Regarding "Other Comments Or Suggestions”:**
* The reviewer mentioned that *Line 110 is only valid for a discrete state space*. We would like to clarify that our system does not impose any constraints on whether the state space is discrete or continuous. In fact, we explicitly allow a multi-dimensional continuous state space, i.e., $S\in \mathbb{R}^d$, as stated in Line 115-116. We recognize that the definition in Line 110 might be somewhat misleading, as $p$ actually refers to the transition kernel in the MDP and is not a probability mass function. We believe it would be clearer to revise the current statement to $p:\mathcal{S} \times\mathcal{A}\rightarrow\mathcal{S}$, and we hope this revision will help clarify the matter.
* We sincerely appreciate the reviewer's feedback, and will include detailed definitions of B-splines and wavelets in the final version of our paper for completeness.
**Regarding Assuption A.1 (d) (i):**
We appreciate the reviewer’s question regarding the ease of satisfying this assumption. A special case that may help clarify the strength of this assumption is when $\pi$ is deterministic, $b$ is the $\epsilon$-greedy policy with respect to $\pi$ satisfying $\epsilon \leq 1 - \gamma^2$, and $\mu=\nu_0$. In this case, Assumption A.1 (d)(i) can be shown to be naturally satisfied (see Sec C.1 of the supplementary material of Shi et al. (2021b) for proof details).
We recognize that this is a somewhat non-intuitive assumption, and the verification may require some calculations. We also appreciate the reviewer’s suggestion to explore whether and how this assumption could be simplified by incorporating the specific form of $\Phi$ and the moving behavior distribution $b(a|s)$. Checking whether the LHS of this assumption is positive-definite (or finding an easier-to-understand sufficient condition for it) essentially requires us to quantify the positive definiteness of the matrix part, i.e., $\xi\xi^\top -\gamma^2 u_\pi u_\pi^\top$. The multiplication by $b(a|s)$ and $\mu(s)$ is more of a weighting method to determine whether the matrix, after taking the expectation, remains positive-definite, which is not the main focus. Thus, deriving a boundedness assumption for $\mu$ from below seems implausible. We would greatly appreciate any further thoughts or ideas you may have on this aspect and look forward to your suggestions.
Once again, we sincerely appreciate your time reviewing our paper and welcome any further questions or discussions. | Summary: The paper analyzes the problem of policy evaluation in the presence of missing data. The authors distinguish between two types of missing data:
- **Missing at Random (MAR):** Data is missing independently of unobserved factors.
- **Missing Not at Random (MNAR):** Data is missing due to a hidden cause, introducing bias in the value function and preventing the actor from completing the trajectory.
### Methodology
To address the policy evaluation problem under MNAR conditions, the authors propose an importance sampling (IS) correction method. Their estimator, **V-IPW**, is shown theoretically to be consistent (converging to the true value) and unbiased, whereas the standard estimator **V-CC** suffers from bias.
The importance sampling estimator relies on a **dropout propensity parameter**, which represents the probability of data being missing given the current state. The authors also propose a principled method to estimate this parameter when it is not known a priori.
### Experimental Evaluation
The authors evaluate their estimator, **V-IPW**, against the baseline **V-CC** in two different settings:
1. **Simulated Environment:**
- The dropout propensity is known.
- A single target policy is evaluated.
2. **Real-World Environment:**
- The dropout propensity is unknown.
- Four different target policies are evaluated: Behavior, DQN, Dueling DQN, and BCQ, all learned via offline reinforcement learning (RL) algorithms.
### Results
The experimental results demonstrate that the **V-IPW estimator** corrects the bias introduced in **V-CC**, effectively compensating for the dropout effect.
Claims And Evidence: While the theoretical analysis of **V-IPW** and **V-CC** is comprehensive and well-structured, the empirical evaluation is somewhat limited.
In the **real-world environment**, there is no ground truth available for the value function. As a result, the comparison between **V-IPW** and **V-CC** relies on the assumption that **V-CC is negatively biased**—but the extent of this bias remains unclear. A more detailed analysis quantifying the potential bias in **V-CC** would strengthen the empirical claims.
Methods And Evaluation Criteria: The purpose method makes sense as Importance sampling is widely used in the RL literature.
Theoretical Claims: The claims and arguments in the theoretical analysis of V-IPW and V-CC make a lot of sense, but I did not validate the correctness of their proofs.
Experimental Designs Or Analyses: The experiments demonstrate the effectiveness of the proposed algorithm. However, there are several limitations in the evaluation:
- **Low-Dimensional Settings:** All experiments are conducted in low-dimensional environments, making it unclear how well the method generalizes to more complex, high-dimensional settings.
- **Propensity Accuracy Analysis:** The synthetic experiments lack an analysis of the accuracy of the estimated propensity scores, which is crucial for understanding the reliability of the importance sampling correction.
- **Limited Environment Diversity:** The algorithm is tested on only a few environments, making it difficult to assess its robustness and general applicability. A broader evaluation across diverse environments would strengthen the claims.
- **Analysis of the important samples requirements:** The algorithm relies on the importance sampling to add weight to rare samples, however, an analysis of how many such samples are needed is missing, this analysis has significant ramifications on the applicability of the proposed algorithm.
Supplementary Material: Briefly
Relation To Broader Scientific Literature: The reinforcement learning setting and problems discussed in this paper are closely related to causal machine learning and uplift modeling.
Essential References Not Discussed: The related work section provides a comprehensive overview of the literature on off-policy evaluation.
Other Strengths And Weaknesses: ### Strengths
1. An algorithm that tackles an issue that was not referenced in the literature before
2. The theoretical analysis and presentation is thorough
### Weaknesses
1. Limited Scope of the Algorithm:
- The proposed method focuses on bias correction in policy evaluation but does not claim to improve the convergence rate over **V-CC**.
- Enhancing convergence could potentially reduce data collection constraints, making the approach more practical for real-world applications.
2. Dropout Propensity Estimation is Deferred to the Appendix:
- The estimation of **dropout propensity** is a critical component for applying the algorithm in real-world settings.
- Given its importance, this section should be discussed in greater detail in the main text rather than being relegated to the appendix.
Other Comments Or Suggestions: No
Questions For Authors: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Response to "Summary-Claims And Evidence”:**
The reviewer raised a concern that *the comparison between V-IPW and V-CC relies on the assumption that V-CC is negatively biased.* Actually, Our real-world experiment consists of two parts: the first (Table 2) is based on the original sepsis dataset, while the second (Table 3) is derived from a quasi-real dataset where we controlled only the dropout hazard function, ensuring it follows a known form. We would like to emphasize the following points:
* In the offline dataset, where the true dropout pattern is unknown, there is no ground truth for the true value function under no dropout. This means we cannot directly assess the bias in V-CC or definitively validate the extent to which V-IPW corrects it. Our inference in Table 2 is based on common knowledge and the intuition that V-CC may underestimate the value function due to early discharge, though we acknowledge that this inference lacks definitive empirical support. We appreciate the reviewer’s attention to this issue, which motivated our quasi-real data analysis using MIMIC-III, as presented in Table 3.
* In Table 3, we explicitly controlled the dropout hazard model using the function $\lambda(\cdot)$, specified above Sec 7, which follows a functional form inspired by prior MIMIC-III studies (Kramer & Zimmerman, 2010; McWilliams et al., 2019). This setup allows us to obtain an unbiased estimate of the value function under no dropout (reported in the first row), serving as a ground truth for comparison. The results in Table 3 consistently show that V-IPW outperforms V-CC in correcting the underestimation bias caused by missing not at random (MNAR) dropout.
**Response to "Summary-Experimental Designs Or Analyses”:**
1. Regarding the "Propensity Accuracy Analysis", we have provided additional support to validate the accuracy of the dropout model estimation in https://anonymous.4open.science/r/OPE_MNAR_ICML_rebuttal-832D/, where the first plot shows small MSEs close to zero, and the second plot compares the estimated parameters to their true values. Additionally, as all V-IPW experiments under MNAR require prior propensity score estimation, Figure 2 and the last two rows of Table 1 (MNAR (P) and MNAR (SP)) in the main paper confirm the accuracy of these estimations through bias, standard error, and empirical coverage probability. Without stable estimation results, the statistical properties of the value function would not hold. We hope the added accuracy analysis regarding the propensity score, along with the existing tables and figures in the main paper, will help address your concerns regarding the dropout function estimation performance.
2. Regarding the "Low-Dimensional Settings" and "Limited Environment Diversity": we sincerely appreciate the reviewer's suggestion on trying more diverse simulation settings and environments to possibly test the wider applicability of our approach. Due to time limit, we might not able to provide another group of setting and detailed analysis during this rebuttal time, but we will incorporate more settings to the final version of our paper.
3. Regarding the "Analysis of the important samples requirements": We appreciate the reviewer's question regarding the sample requirements in order to guarantee a stable estimate of the value function. Based on the asymptotic results in Theorem 4.7, the sample size requirement actually can be derived with a few steps. Here due to space limit we provide a brief analysis about the requirement, and we will add it to the final version of our paper to help with it. As $\hat{V}^{\pi}\sim \mathcal{N}(V^{\pi},\hat{\sigma}^2/(nT))$ (for simplicity we omit $\mathbb{G}$ in parenthesis and the subcript 'IPW'), applying Gaussian tail bounds we have $\mathbb{P}(|\hat{V}^{\pi}-V^{\pi}|\geq \epsilon)\leq 2\exp\\{-nT\epsilon^2/(2\sigma^2)\\}$. Therefore, to achieve an error bound $\epsilon$ with probability at least $1-\delta$, the required sample size would be $n\geq \log(2/\delta)\cdot 2\sigma^2_{\pi}/(\epsilon^2T)$. For example, by setting $\delta = \epsilon = 0.01$, $T = 100$, and $\sigma^2_{\pi} = 0.5$ (a value comparable to the simulation setting), we find that $n \geq 530$ trajectories would suffice.
**Response to Weakness 1:**
Although we did not explicitly state the convergence rate of V-IPW, it is provided by the asymptotic normality result in Theorem 4.7, which shows that $\hat{V}^{\pi}$ converges to the true value at a rate of $O(n^{-1/2}T^{-1/2})$. This ensures fast bi-directional convergence in both $n$ and $T$, and this rate matches the parametric convergence rate, leaving no room to further improve the order of convergence.
**Response to Weakness 2:**
Thank you for your suggestion. We agree and will reintegrate the dropout propensity section into the main text to enhance readability and clarity.
Once again, we appreciate your time and effort in reviewing our paper and look forward to your questions for further discussion. | Summary: This paper studies OPE when trajectories are truncated/missing and the missingness is non-ignorable. A new estimator based on inverse probability weighting is proposed, with theoretical justification for its unbiasedness and consistency properties. Experiments were conducted on a synthetic and a semi-synthetic problem to show how proposed approach compares with baseline approach that assumes complete data.
## Update after rebuttal
I am maintaining my already positive recommendation.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I looked at the main text theorems and they appear to make sense. I did not read Sec 4.3 shadow variables carefully as I am not too familiar with that concept.
Experimental Designs Or Analyses: Yes, the experiments are described with necessary details.
Supplementary Material: No.
Relation To Broader Scientific Literature: This paper addresses an important issue in OPE on real data which is often overlooked by assuming complete data.
As it touches on multiple areas, terminologies from different areas are being used. For example, MAR/MNAR, ignorable/nonignorable misingness. I think it is important to clarify these upfront, and also acknowledge other possible interpretations of the same phenomenon: e.g. trajectory truncation (as an alternative phrase for monotone missingness), or censoring (from survival analysis, example would be early ICU discharge).
Essential References Not Discussed: Not to my knowledge.
Other suggested citations:
- Ji et al. Trajectory Inspection: A Method for Iterative Clinician-Driven Design of Reinforcement Learning Studies. AMIA 2021. This paper also investigated the early discharge / early termination issue in MIMIC dataset.
Other Strengths And Weaknesses: - Overall the paper is well written.
- Perhaps in the introduction it should be made clearer what type of missingness is being addressed, especially in an MDP setting. L14-right "offline data is often incomplete due to different types of missingness" - at this point, it's unclear what is missing, is it the states/observations, actions, or rewards, or some combination.
Other Comments Or Suggestions: None. See comments above.
Questions For Authors: None. See comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks for your thoughtful questions and the time you spent reviewing our paper. We really appreciate your insights and are
happy to discuss any further ideas or questions you may have.
**Clarification on Terminology:**
We sincerely appreciate the reviewers' feedback on clarifying terminology across different fields, particularly regarding the comments on *Relation to Broader Scientific Literature*. We will provide thorough definitions of concepts such as monotone missingness and censoring in the introduction or at their first occurrence to enhance readability and coherence throughout the paper.
**Regarding Essential References Not Discussed:**
Thank you for highlighting the related work by Ji et al. (2021) on early discharge in the MIMIC-III dataset. After a careful review, we notice that their study primarily applies RL methods to identify potential issues with the existing vasopressor treatment policy. Notably, part of their findings aligns well with our problem motivation, which demonstrates that early discharge can introduce significant modeling bias, thereby impacting evaluation. We will incorporate this reference into the introduction, as it further substantiates the motivation behind our work.
**Clarification on Types of Missingness in the Introduction:**
We acknowledge that Line 14 may be somewhat vague in discussing different types of missingness, which could be unclear to readers. Here, the missingness types (as introduced in the subsequent paragraph) include both MAR and MNAR, specifically concerning the observation status of the reward being evaluated. Within the RL framework, this missingness affects both the reward and next-state, denoted as $(R_{t+1}, S_{t+1})$. Given the presence of non-ignorable missingness, the absence of $(R_{t+1}, S_{t+1})$ naturally leads to cascading missingness in subsequent state-action-reward sequences. While a detailed explanation may not be feasible in the introduction, we will clarify in Line 14 that the missingness primarily pertains to the reward in general settings. We hope this could ensure greater clarity for readers.
**Finally**, We sincerely appreciate your time and effort in reviewing our paper and look forward to your questions and further discussion. | Summary: The paper proposes the challenge of non-ignorable missing data in policy evaluation in reinforcement learning, which is the type of missingness that has dependency with the reward and next state value. The intuition for the significance of the problem and its applications in practice is well explained. Moreover, a method for estimating the value function in the presence of such an issue is proposed, and its unbiasedness is proved. The method's effectiveness is also justified by numerical and practical experiments. The main idea is fairly simple and easy to understand, and appears effective in the case of the non-ignorable missingness.
Claims And Evidence: The major claims of the study are as follows:
1. The concept of ignorable/non-ignorable missingness in OPE and the unbiasedness of the simple Monte-Carlo average for value estimation in the case of ignorable missingness.
2. A value estimation method that remains unbiased even when the missing data is non-ignorable.
3. Unbiasedness and asymptotic distribution of the proposed estimation.
4. Empirical experiments on both synthetic and real-world datasets that support the effectiveness of the proposed method.
5. There are claims for *traditional* OPE methods compared to the proposed method, such as the biasedness in MNAR and unbiasedness in MAR. *The traditional methods* in the paper, however, are limited to CC. There is a vast range of off-policy evaluation methods in the literature, at least 7 of them I'm aware of (PM, ES, IX, OS, LSE, IPS-TR, LS). I suggest that the authors explicitly define that their analysis and comparison on only on the CC and IPW(proposed) methods.
Methods And Evaluation Criteria: The evaluation in synthetic experiments is based on ECP and MSE, which are standard and appropriate.
For the real-world experiments, the real value function is not known, and the true value is hence not identifiable. This is especially more problematic in the presence of non-ignorable missing data. Therefore, in the setting provided in these experiments, a discussion on the estimated value is apparently the most that we can do.
I'm not sure if it is possible or not, but an experimental setting where the missingness happened naturally (not synthetically), but the best policy is trivial, and hence the true value function is known, can be added to provide a more confident evidence of the model's effectiveness on arbitrary, complex, unknown missed-data mechanisms.
Theoretical Claims: The theoretical claims are sound and proven mathematically, and I don't find any fault in this part.
Experimental Designs Or Analyses: The comparison is limited to CC method, which is a very trivial and naive method. Other OPE methods should also be included in the experiments. These are some, but not all of them:
[1] Dudík, Miroslav, John Langford, and Lihong Li. "Doubly robust policy evaluation and learning." arXiv preprint arXiv:1103.4601 (2011).
[2] Metelli, Alberto Maria, Alessio Russo, and Marcello Restelli. "Subgaussian and differentiable importance sampling for off-policy evaluation and learning." Advances in neural information processing systems 34 (2021): 8119-8132.
[3] Behnamnia, Armin, et al. "Batch Learning via Log-Sum-Exponential Estimator from Logged Bandit Feedback". ICML 2024 Workshop: Aligning Reinforcement Learning Experimentalists and Theorists, 2024, https://openreview.net/forum?id=dT6pUWzSZM.
[4] Wang, Yu-Xiang, Alekh Agarwal, and Miroslav Dudık. "Optimal and adaptive off-policy evaluation in contextual bandits." International Conference on Machine Learning. PMLR, 2017.
[5] Sakhi, Otmane, et al. "Logarithmic smoothing for pessimistic off-policy evaluation, selection and learning." arXiv preprint arXiv:2405.14335 (2024).
Supplementary Material: The supplementary material consists of the proof of the theorems and a set of additional experiments.
Relation To Broader Scientific Literature: Missing data in OPE is a key challenge and in practice, it occurs very often. In the medical field, the fact that patients' status is mostly not completely tracked makes almost every subject (trajectory of treatment) incomplete. In recommendation systems, the delayed reward observation is the major source of missing data.
Essential References Not Discussed: The following paper investigates missing-not-at-random data in ope.
[1] Takahashi, Tatsuki, Chihiro Maru, and Hiroko Shoji. "Off-Policy Evaluation for Recommendations with Missing-Not-At-Random Rewards." arXiv preprint arXiv:2502.08993 (2025).
[2] Yang, Longqi, et al. "Unbiased offline recommender evaluation for missing-not-at-random implicit feedback." Proceedings of the 12th ACM conference on recommender systems. 2018.
There are also other papers that investigate missing-not-at-random data like the following,
[3] Wang, Zifeng, et al. "Information theoretic counterfactual learning from missing-not-at-random feedback." Advances in Neural Information Processing Systems 33 (2020): 1854-1864.
Other Strengths And Weaknesses: 1. There is an assumption that the first sample of the trajectory is never missing. This limits the application of the proposed method in OPE for the bandits, as a bandit problem is an RL problem with trajectories of length 1. So, the method cannot be used for missing data in the bandit learning and evaluation problems.
2. There are some implicit assumptions at are not discussed. They should be implicitly stated as assumption, and justified by evidence and discussion, these are the ones that I found doubtful, implicit and ignored.
* uniform boundedness on reward values
* Action-state linear separability in the model of the Q-function.
3. The proposed challenge is very significant, and the proposed method is also intuitive and easy to accept as a working method. There are also some initial theoretical findings and base experiments. However, it appears that it has much work to do to become a complete study that meets ICML standards.
* Comprehensive comparisons with the OPE methods in the literature are required.
* The form of the missing mechanism can be investigated, and more real-world experiments with complex, unknown missing data procedures should be added that can be actually validated. Also, more settings for synthetic experiments can make the paper richer and the claims more persuasive.
* The idea of IPW is used in many different contexts in OPE and OPL (for example, in average treatment effect literature), hence either the extensive practical or theoretical analysis can solidify the contributions of the paper.
* A learning-based model-free method is necessary for large-scale applications and complex environments.
* The estimation of $\lambda$, the dropout probability, is not fully handled, and it's not clear how it can be done in an arbitrary problem. It needs more investigation and analysis. Also, theoretical analysis in the presence of estimated, inaccurate $\lambda$ should be added to justify the method in practice.
Other Comments Or Suggestions: I stated my suggestions in the Strengths and Weaknesses section.
Questions For Authors: 1. What is the advantage of the proposed method compared to other methods that handle missing data, such as the following,
[1] Takahashi, Tatsuki, Chihiro Maru, and Hiroko Shoji. "Off-Policy Evaluation for Recommendations with Missing-Not-At-Random Rewards." arXiv preprint arXiv:2502.08993 (2025).
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | null | null | null | null | null | null | |
PokéChamp: an Expert-level Minimax Language Agent | Accept (spotlight poster) | Summary: This paper introduces PokeChamp, and LLM combined with a game-playing agent to perform minimax search for winning Pokemon battles. The authors replace several parts of minimax search with an LLM and introduce a Pokemon battling dataset to understand LLM agent's failures. PokeChamp is able to reach the top 90% of human performnace.
Claims And Evidence: See strengths and weaknesses
Methods And Evaluation Criteria: See strengths and weaknesses
Theoretical Claims: See strengths and weaknesses
Experimental Designs Or Analyses: See strengths and weaknesses
Supplementary Material: See strengths and weaknesses
Relation To Broader Scientific Literature: See strengths and weaknesses
Essential References Not Discussed: See strengths and weaknesses
Other Strengths And Weaknesses: # Strengths
- The paper provides an interesting exploration of how to use LLM agents for partially observable games. There are several ideas that were explored that could point towards future paths to understanding how to mix LLMs with more classical AI systems.
- It is clear that the authors enjoyed creating their agent, which makes the paper fun to read.
- The authors collected a dataset which will greatly help enable progress towards studying partially observable games. Moreover, the authors use the dataset to quantify their agent's performance.
# Weaknesses
- **The LLM does not appear to be well utilized:**
- The LLM appears in the one-step lookahead when estimating the opponent's stats, the opponent's action prediction, and the value function. In the first case, it appears that the estimating the opponent's stats from data likely can be learned from data and does not require a language prior. In the second case, the authors show that the LLM's performance is slightly above random (although this could possibly be due to Pokemon data being OOD for the LLM), and in the third case there is no evidence that the LLM's estimation of the value function is actually accurate (although I realize that this is difficult to evaluate).
- While I think this work is still interesting as an exploration of how to combine LLMs with agents, I don't think the Pokemon setting is particularly illustrative for showcasing the strengths of the LLM. Much of this work could be done with standard DNNs.
- No ablation studies of the agent: would it be possible for the authors to ablate some of the LLM components of the agents to see where the performance gains are coming from? Some suggestions: a) replace the LLM in the stat estimation with a trained NN, b) remove the LLM from the action prediction (randomly predict an action or train a NN to predict the action), or c) use smaller LLMs, e.g., Llama-3.2-3B. How much does this tank performance?
- No studies of the agent's value function: although I realize that it's extremely difficult to even empirically estimate the value function, could the authors speak to the quality of the estimated value function produced by th eLLM?
Other Comments Or Suggestions: Nit: change GPT 4-o to 4o everywhere (I noticed this in the abstract) and change Llama3.1:8b to Llama-3.1-8B (L320). Also are you using the instruct version? If so that should be mentioned.
Questions For Authors: Is 90% ELO good in an absolute sense? I wonder if there's just not many people playing Pokemon battles or the average skill level of human players is pretty low. I'm guessing it would take someone much more time to get 90% at chess than at Pokemon battles. Do you have a sense of the difficulty of the accomplishment? (I still think it's a cool result regardless but it's a bit abstract for me).
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for recognizing the value of our exploration of LLM agents for partially observable games and appreciating our dataset contribution. These are indeed core strengths of our work.
**LLM utilization**: LLMs are key components in our system to achieve the claimed performance. Our work represents an important attempt to effectively utilizing LLMs in complex two-player game environments: While opponent stat estimation could potentially be learned from data alone, LLMs provide crucial domain knowledge that would otherwise require extensive labeled data and model training. For instance, they understand type matchups, move effectiveness, and Pokemon meta-strategies with minimal prompting (as shown in Figure 5, page 6, where PokéChamp adapts to complex mechanics like Terastallization and Dynamax). The one-step lookahead mechanism combines LLM knowledge with damage calculations to determine the best action for the game by extrapolating over short horizon information.
While opponent action prediction is challenging (13-16% accuracy for min-player, Table 1, page 5), this is still valuable for narrowing the search space in minimax and substantially better than random (which would be <1% given the large action space). Even imperfect opponent modeling significantly improves overall performance, as demonstrated by our 76% win rate against the strongest LLM-based bot and 84% against the strongest heuristic bot (Table 3, page 7).
**Pokemon as illustrative settings for LLM**: Pokémon battle is a text-based two-player game featuring a vast pool of Pokémon, types, items, moves, and game mechanics, all described in text, resulting in a combinatorial explosion of possible configurations. It exemplifies a complex, partially observable environment with a massive state space (~10^354 for the first turn alone, page 2). This complexity makes it an excellent testbed for demonstrating how LLMs can constrain search to human-like strategies without explicit training, which is our core contribution.
**ablation studies**: We appreciate this suggestion. We do provide a partial ablation by comparing PokéChamp with GPT-4o versus Llama 3.1:8b (Tables 3-4, page 7-8), demonstrating that our approach works well even with smaller models. Though frontier models such as GPT-4o perform best. We also compare against the One Step Lookahead agent without the full minimax framework (Tables 3-4), showing the value of our complete approach.
Regarding the value function quality, as mentioned in our initial response, the best evaluation is performance in games. Our expert-level performance (1500 Elo rating, top 10%, Figure 1, page 1) demonstrates the effectiveness of our value function approximation. The value function is able to correctly prioritize actions that lead to winning strategies, as shown by our significantly higher win rates compared to all baselines.
**the significance of 90% Elo**: Pokémon Showdown is a very active competitive ladder with roughly 3000 active games at any given time, and over millions of games occurring every month. This makes the top 10% achievement substantial. Reaching this level requires deep understanding of complex strategies, team compositions, and meta-game knowledge. The 1500 Elo rating on Pokémon Showdown is considered expert-level play among the community.
We thank you for your suggestions regarding model naming conventions and will address these in our revision. | Summary: The paper introduces PokéChamp, an agent that leverages minimax-based search to play competitive Pokemon battles. Specifically, the LLM performs action sampling, opponent modeling and state value calculation, allowing it to navigate partially observable state spaces of the battles. The authors also present various experiments in the paper showcasing that PokéChamp outperforms existing LLM-base and heuristic bots built for Pokemon battles.
Claims And Evidence: The claims in the paper are largely well supported. For instance, many experiments were conducted and empirical results showed that PokéChamp outperforms existing rule-based bots and LLM-based agents under various different conditions when measuring win rates, with the measured Elo ratings also reinforce these results.
However, the claim in the conclusion that this paper provides a generalized framework for other POMGs lack empirical evidence. The design of PokéChamp is highly specific to the mechanic of Pokemon battles, and hence while the framework is sound in theory, it is hard to tell how generalizable this method will be to other games.
Methods And Evaluation Criteria: The methods used do make sense for the application at hand. By integrating the three main minimax search steps: action sampling, opponent modeling and state value calculations, the agent can optimize decision making in the complex, partially observable environment. The one-step look ahead also helps improve decision making the estimating the immediate consequences of the potential actions, enabling PokéChamp to further improve the decisions made.
The evaluation that include comprehensive benchmarks against well known Pokemon bots and human players under diverse settings (which sometimes isolate particular game mechanics to test the agent’s understanding of those in particular) is robust. The metrics measured such as win rate and Elo are strong quantitative measures of the performance.
Theoretical Claims: The paper formulates Pokemon battles as partially observable Markov game (POMGs), but there are no explicit theoretical claims of proofs. In general, there is a slight gap between the theoretical game theory framework and the LLM generated value functions used in PokéChamp, as it is unclear how certain theoretical properties translate when using LLM-based approximations of the values.
Experimental Designs Or Analyses: The battles that are conducted in the experiments span multiple setups and compare multiple baselines bots and human players to PokéChamp, providing a comprehensive evaluation. The metrics such as win rate, Elo and average number of turns are suitable measures of the performance of the framework.
The analysis of the weak points of PokéChamp (such as losses due to time, or handling stall tactics and excessive switching) were insightful in identifying what the limitations are and where the framework could be improved.
Supplementary Material: Yes I briefly reviewed the appendix, it provided additional information regarding the details on the game mechanics and technical details of Pokemon battles and the experiment setup, additional puzzle scenarios and additional experiments and results. They provide a deeper understanding of the setup and more supporting empirical validation to the main results.
Relation To Broader Scientific Literature: The paper builds on the idea of developing AI that achieves superhuman performance in games, it draws reinforcement learning approaches from work such as AlphaZero, and extend those ideas by integrating LLMs into the framework to reduces the expensive training required in the existing frameworks. It also improves the research on other LLM based agents such as PokéLLMon by incorporating these planning algorithms. The combination of the two methodologies introduces ideas that can be used in further research, and are especially practical due to the lack of extensive training requirements.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- The paper presents a novel framework to integrate minimax search algorithms with LLM agents, enabling improved performance without the massive training requirements
- PokéChamp outperforms existing bots and agents across many benchmarks and battle configurations, proving its efficacy
Weaknesses:
- The biggest weakness of this paper is the limited generalization it has to other applications. Many components of PokéChamp are highly specific to Pokemon limits the ability for this framework to be easily applicable to other games without significant additional configurations (unlike more general RL based methods that can be generalized with less effort)
- Opponent modeling is mentioned as a key component of the framework, however the prediction accuracies are very low (13-16%) and hence more analysis into this step would be helpful to investigate the effectiveness of it
Other Comments Or Suggestions: N/A
Questions For Authors: - Can the authors speak more about the trade-offs associated with search depth and what their approaches are to optimize this balance?
- Can the authors speak more generally about the generalization of these methods beyond Pokemon battles?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for highlighting our framework's novelty and effectiveness in integrating minimax search with LLMs, and for recognizing PokéChamp's strong performance across multiple benchmarks.
**generalizability beyond Pokémon battles**: Our framework naturally applies to any two-player zero-sum competitive games beyond Pokemon where minimax tree search is feasible. As described in Section 3 (page 3-4), our framework implements three LLM-powered components that can generalize to any POMG: "(1) Action sampling via LLM and tool-assisted action generation, (2) Opponent modeling through historical data and LLM-based prediction, and (3) LLM-generated value function for leaf nodes. This method implements basic components of the minimax search tree with LLM predictions that can generalize to any POMG."
The core innovation here is the replacement of traditional minimax components with LLM-based alternatives. While we demonstrate this in Pokémon, the structure is applicable to any two-player partially observable game where states can be described in natural language. Unlike RL-based methods that require extensive task-specific training, our approach only requires observation space descriptions in natural language. This makes implementation no more difficult than developing custom RL environments and reward functions.
**search depth trade-offs**: As detailed in Section 5.3 (page 7), we implement strict time management to comply with the 15-second per turn limit: "Our search depth is limited by the 15 second time cutoff, which is a maximum of a two step lookahead with a branching factor of 16 (4 max player actions, 4 min player actions)." We address this trade-off dynamically throughout gameplay, as "the decision time when there is only 1 pokemon left is very fast due to the limited number of states to expand." This demonstrates our system's adaptability to different computational constraints.
**opponent modeling accuracy**: While the raw prediction accuracies (13-16%) may appear low, this reflects the inherent challenge of predicting exact moves in a complex, partially observable environment with a large action space. Importantly, even imperfect opponent models provide significant value in minimax search by narrowing the branch exploration to more likely opponent responses. The comparative performances against state-of-the-art bots (76% win rate against the strongest LLM-based bot and 84% against the most advanced heuristic bot) demonstrate that our opponent modeling is effective despite these challenges.
We appreciate your overall positive assessment of our work and hope our clarifications address your concerns about generalizability and search depth optimization. | Summary: This paper introduces PokeChamp, an LLM-powered game-theoretic agent designed for competitive Pokémon battles. PokeChamp uses LLM-guided minimax search to model decision-making in partially observable environments. It outperforms all prior LLM-based and heuristic-based Pokemon bots.
## update after rebuttal
The authors address most of my concerns, and I keep my original rating to lean toward accepting the paper.
Claims And Evidence: 1. The overhead of LLM-based search is not fully discussed, particularly its impact on real-time play.
2. While PokeChamp achieves the 90th percentile, there is a concern that a small fraction of players may be truly active. A comparison specifically with active players would provide a more realistic performance benchmark.
Methods And Evaluation Criteria: The paper introduces Pokemon battle-specific terms (e.g., "Abyssal bot", "Elo") without detailed explanation or references. This makes the work less accessible to researchers unfamiliar with Pokémon battles.
Theoretical Claims: Not much theory is included in this paper.
Experimental Designs Or Analyses: Sensitivity to hyperparameters (e.g., search depth) is not explored.
Ablation studies on the effectiveness of each component are missing.
Supplementary Material: The authors provide the online code link in the abstract, but if you want to see the code, then the link is not "anonymous for review" and directly shows the author names.
Relation To Broader Scientific Literature: Missing some discussion about related papers. see "Essential References Not Discussed".
Essential References Not Discussed: The idea of integrating LLMs with the minimax search framework for game-playing agents is closely related to prior work by Guo et al. (2024), which explores a similar concept in two-player zero-sum games. Guo, Wei, et al. "Minimax Tree of Thoughts: Playing Two-Player Zero-Sum Sequential Games with Large Language Models." ICML 2024 Workshop on LLMs and Cognition.
Other Strengths And Weaknesses: **Additional Weaknesses:**
Prediction accuracy at higher Elo ratings: In Table 1, action prediction accuracy is highest at the 1800 Elo stage. Can the authors explain this phenomenon? Are skilled players' actions easier to predict?
Damage calculator inconsistency: In Appendix line 685, "dragondarts: 161 turns to KO Primarina" seems incorrect, as Primarina is Fairy-type and should be immune to Dragon-type moves. How does the damage calculator work?
Other Comments Or Suggestions: See weaknesses and questions.
Questions For Authors: 1. Can you go deeper into the online evaluation score, such as Elo? While PokéChamp achieves expert-level performance (90th percentile Elo), how does it compare to active players?
2. Can you provide the trend of decision time as the round progresses? At which step does the LLM’s response time exceed 15 seconds?
3. PokeChamp implements three LLM-based components (action sampling, opponent modeling, value estimation). Are these components specifically designed for Pokemon battles, or do they or their intuition have broader applicability?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful review. We appreciate your recognition of PokéChamp's strong performance against prior bots and human players.
**Elo ratings and active players**: The Elo system on Pokémon Showdown (which we use for evaluation) only includes active players by design. Inactive accounts are reset to a base Elo of 1000 regularly and are not included in the percentile, ensuring our 90th percentile achievement reflects performance against the current active competitive community. As detailed in Figure 1 (page 1), PokéChamp's 1500 Elo rating places it firmly among expert players in this active ecosystem. This is comparable to how chess platforms like chess.com evaluate player performance. Pokemon Showdown has a smaller scale: roughly 3000 active games at any given time with millions of games played every month.
**LLM overhead in real-time play**: We address this important constraint in Section 5.3 (page 7), noting that "33% of games were lost due to time constraints." Our system implements strict time management to ensure compliance with the 15-second per turn limit, which restricts our search depth to a maximum of two-step lookahead with a branching factor of 16 (4 max player actions, 4 min player actions). In practice, the decision time varies based on game state complexity significantly faster when fewer Pokémon remain in play due to the reduced state space. We have further developed a faster version of this using better coding practices and systems techniques to increase speed that we will release with our code that achieves the same performance as mentioned in the paper.
**Pokémon-specific terms**: We agree that better explanation of Pokémon-specific terms would improve accessibility. Elo is a standard rating system widely used in competitive gaming beyond Pokémon (originated in chess), and we define the Abyssal bot in Section 5.1 (page 6) as "a rule-based heuristic bot used in official Pokémon games." We'll expand these definitions in the revised version.
**Higher prediction accuracy at 1800+ Elo**: This interesting observation likely stems from the narrower strategy space employed by elite players. At this high level, players tend to favor optimal, established strategies rather than unpredictable or sub-optimal plays, making their decisions more consistent and thus more predictable.
**Damage calculator**: The damage calculator example you noted (dragondarts: 161 turns) is actually a technical implementation detail. We cap the maximum turns to KO for cases where a Pokémon is effectively immune to an attack (as with Dragon-type moves against Fairy-types). By avoiding infinite values, we find that the LLM performs better at understanding and comparing all options.
**Three LLM-based components**: Our three LLM-based components (action sampling, opponent modeling, and value estimation) form a general framework that is naturally applicable to any two-player partially observable game, not just Pokémon. These components could be adapted to other strategic games with similar characteristics.
**Remaining comments**: We will address the missing ablation studies and hyperparameter sensitivity analysis description in our revised manuscript. We provide a link to a double-blind project website within our submitted project. The code link within the website is already announced “not for anonymous review” during the review period, but is available to reviewers after the review period is over. Thank you for your valuable feedback that will help us improve the final version.
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Rebuttal Comment 1.1:
Comment: Thanks to the authors for the detailed response to the concerns. I have no other concerns and think this work brings a contribution to the related community. So I keep the positive rating. | Summary: The authors introduce a novel RL agent that integrates and LLM into the tree-search process showing that their method can provide acceptable decisions in complex game states.
Claims And Evidence: The authors claim that their method is SOTA on pokemon which they test in multiple ways and against multiple other models. This is a clear and strong evidence for the claim.
Methods And Evaluation Criteria: Elo and winrate are not perfect metrics of RL search performance, but are the standard in these types of zero-sum games. So I don't have an issue with the evaluation. I would have liked some more detailed analysis of the model's behaviour (beyond section C), for example it might be exploiting defects in the other models, or taking very unusual lines against humans leading to an inflated winrate.
Can the model output a probability distribution over possible moves (policy map)? Looking at perplexity on a dataset of human moves, or the sharpness of the distribution would reveal more about the underlying reasoning.
Theoretical Claims: N/A, this is empirical work
Experimental Designs Or Analyses: See above, and I am also concerned with the validity of using an LLM as a black box. This significantly reduces the generalizabilty of the results as we do not know how much of the uplift came from the LLM's prompting, or some components of the LLM's training data (i.e. there are many games online that might have been included).
Supplementary Material: Yes, all
Relation To Broader Scientific Literature: This is relevant to both RL and the larger project of integrating LLMs into task planning. As I said above the black box nature of the work is a sever limitation, but I think this helps highlight ways that LLMs can be used as a component of a larger planning system.
Essential References Not Discussed: No
Other Strengths And Weaknesses: See above
Other Comments Or Suggestions: See above
Questions For Authors: See above
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **More detailed model behavior analysis beyond Section C**: In addition to Section C, our paper provides the following analyses on our model/method with respect to the mechanics and strategies present in this game. In Section 4.3 (page 5-6), we present benchmark puzzles specifically designed to test PokéChamp's strategic decision-making abilities with special mechanics like Terastallization and Dynamax. Figure 5 illustrates how PokéChamp demonstrates understanding of complex type matchups and strategic mechanics usage rather than exploiting defects. Additionally, we evaluate against both bots and human players (Section 5.3), showing that our approach generalizes beyond potential weaknesses in other models.
**probability distribution over possible moves**: We assess this in Table 1 (page 6), where we evaluate action prediction accuracy from Top-1 through Top-5 (ranking according to the action probabilities), effectively showing a distribution over moves compared to actual human actions.There may be multiple valid strategies at any point, which is why we include the Top-K metrics. The player prediction accuracy for PokéChamp varies between 26-30% for Top-1 and improves to 43-66% for Top-5 as Elo increases. We appreciate your suggestion to look at perplexity on human moves, which we can incorporate in future work.
**the "black box" nature of using an LLM**: We have taken great care to make our approach transparent. As illustrated in Figure 2 (page 3), we explicitly replace three components of minimax search with LLM-based generations and clearly explain the contribution of each component. The LLM serves as a prior to constrain the search space to human-like strategies (page 2), leveraging general knowledge rather than Pokemon-specific training. Our ablation studies comparing PokéChamp with Llama 3.1 versus GPT-4o (Tables 3-4) demonstrate that some performance gains come from the intrinsic model capacity. However, we also provide ablations to show that all tested models greatly benefit from our methodology (comparing PokéChamp with PokéLLMon, Tables 3-4). In fact, being able to switch in the latest frontier model or open-source model when new capabilities emerge is an important benefit of this method.
We also demonstrate robustness across different formats (Gen 8 Random Battles, Gen 9 OU) and against human players (achieving 1500 Elo, top 10% of players), showing that our approach generalizes well beyond specific test environments.
Thank you for the positive feedback on our evaluation metrics and recognition of our work's relevance to both RL and LLM integration into task planning. | null | null | null | null | null | null |
The Perils of Optimizing Learned Reward Functions: Low Training Error Does Not Guarantee Low Regret | Accept (poster) | Summary: This paper seeks to characterize the relationship between data distributions over the state-action space of a prescribed Markov decision process (MDP), reward learning from such data distributions, and the resulting regret (which the authors define as normalized suboptimality w.r.t. the true reward function) of optimal policies for the resulting learned reward functions. The core goal of the work can be summed up as characterizing conditions on the data distribution and learned reward error under which large regret is possible, a situation the authors call "error-regret mismatch". The paper develops theoretical machinery to achieve this, first defining the notion of "unsafe" and "safe" data distributions capturing when error-regret mismatch is and is not possible, respectively, then establishing several results characterizing specific conditions on MDPs, data distributions, and learned rewards under which error-regret mismatch occurs. A key result, Theorem 3.5, provides necessary and sufficient conditions under which a data distribution is safe for a given MDP, learned reward error, and regret; the conditions are provided in the form of a matrix inequality (a system of linear inequalities), and tools are provided for explicitly computing the associated matrix in Appendix C when the MDP is known. Several of the error-regret mismatch results are extended to the regularized MDP setting and connections to reinforcement learning from human feedback (RLHF) are discussed in detail.
Claims And Evidence: *Are the claims made in the submission supported by clear and convincing evidence? If not, which claims are problematic and why?*
Yes. See Strength 1 from **Strengths and Weaknesses** section below.
Methods And Evaluation Criteria: *Do proposed methods and/or evaluation criteria (e.g., benchmark datasets) make sense for the problem or application at hand?*
Yes, the theoretical methods and criteria proposed make sense.
Theoretical Claims: *Did you check the correctness of any proofs for theoretical claims? Please specify which ones, and discuss any issues.*
Yes: Sections 3 & 4 in detail, skimmed those of Sections 5 & 6.
Experimental Designs Or Analyses: n/a
Supplementary Material: *Did you review the supplementary material? Which parts?*
I read those of Appendix C and Appendix D through the application of Berge's maximum theorem fairly closely, and skimmed the rest.
Relation To Broader Scientific Literature: The key results from this paper provide a theoretical framework for studying the relationship between data distributions and suboptimality when performing reward learning. Such a framework has been lacking in the reward learning / RLHF literature, to my knowledge. This is of potentially high interest to the community due to the practical importance of RLHF in tuning large language models (LLMs). Beyond the LLM and RLHF communities, addressing questions of data coverage and reward learning are important to the offline RL and inverse RL communities, respectively, and the theoretical machinery established in this paper may prove useful to them as well.
Essential References Not Discussed: None, to my knowledge.
Other Strengths And Weaknesses: **Strengths**
The paper enjoys major strengths:
1. The paper establishes a rigorous and clearly useful theoretical framework for studying the relationship between data distributions and suboptimality when performing reward learning. Such a framework has been lacking in the reward learning / RLHF literature, to my knowledge. Definition 2.1 provides a well-motivated and concrete characterization of "safe"/"unsafe" data distributions, as described in the **Summary** above. The results in Sections 3-6 provide concrete (though somewhat partial, as detailed in **Weaknesses** below) insight into the conditions under which error-regret mismatch occurs. The proofs of the key results provided in the appendix appear to be correct (I read those of Appendix C and Appendix D through D.7 fairly closely, and skimmed the rest) and provide significant additional insight. I especially highlight Theorem 3.5 discussed in my **Summary**: I believe that this result, along with the proof, explicit characterization of the system of inequalities, and algorithm for computing $M$ provided in Appendix C, all provide fundamental and important tools that can likely be used to study the error-regret mismatch problem for specific classes of MDPs in future work; I feel that these results may constitute the most significant contribution of the paper.
2. The quality of the presentation and writing is very high. All contributions, assumptions, and results are clearly stated, thoroughly motivated, and satisfactorily discussed. The limitations of the setup (e.g., the discussion starting line 214, left column, regarding the difficulty of guaranteeing the learned reward error in eq. (1)) and the computational challenges of using some of the results (e.g., potential intractability of computing $M$ in Theorem 3.5, discussed at the end of Section 3) are clearly described. The proofs in the appendix are well-written, well-organized, and sufficient intuition and discussion are provided.
3. The motivation and relevance of this work to the community is very high, particularly due to the practical importance of RLHF in tuning large language models (LLMs), as discussed in Section 6. Beyond the LLM and RLHF communities, addressing questions of data coverage and reward learning are important to the offline RL and inverse RL communities, respectively, and the theoretical machinery established in this paper may prove useful to them as well.
**Weaknesses**
My primary complaint is that two of the key results on "unsafety" of data distributions are not constructive, in the sense outlined below. Specifically, Proposition 3.3 and Corollary 3.4 directly assume the existence of certain classes of policies that can then be shown to force a given data distribution or all data distributions to be unsafe. While this provides a (potentially) useful sufficient condition for "unsafety", it leaves open the question of whether such policies actually exist and is therefore not constructive. It would be more satisfying and clearly useful to have existence results or at least worked examples showing that the sufficient conditions of Prop. 3.3 and Cor. 3.4 do hold under reasonable conditions. I suspect that other results from the paper (e.g., Thm. 3.5 or the $D$ construction from the pf. of Thm. 4.2) could be used to construct such results/examples.
Other Comments Or Suggestions: n/a
Questions For Authors: 1. When might we expect the $\hat{\pi}$ from Prop. 3.3 to exist?
2. When might we expect the policy class $\Pi_L$ from Cor. 3.4 to exist?
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: Thank you for your thorough review! We address your main concern below.
> It would be more satisfying and clearly useful to have existence results or at least worked examples showing that the sufficient conditions of Prop. 3.3 and Cor. 3.4 do hold under reasonable conditions. [...] 1. When might we expect the \hat{\pi} from Prop. 3.3 to exist? 2. When might we expect the policy class \Pi_L from Cor. 3.4 to exist?
This is a reasonable question. We do not yet have concrete theoretical results “constructing” bad policies in general settings, but we think the example in Appendix B.4 provides useful intuitions that one could expand to a general result with further work. In particular, in the example, there are many *equivalent styles* for an LLM to phrase an answer that are all equally bad according to the true reward function (e.g., imagine instructions to build a nuclear weapon in many different languages). If this is the case, then no data distribution can cover *all* of these different styles; intuitively, the distribution has only a total weight of “one” to distribute, and so some styles necessarily get low weight.
We think this could be turned into a general result by assuming an *equivalence relation* on the set of state-action pairs, such that equivalence classes of state-action pairs
- are “large”; in particular, for every fixed state s, and every action a, there exist many equivalent pairs (s,a′) sharing the same state;
- have constant true reward;
- have well-defined (total) transition probabilities to equivalence classes of states.
We believe an example of such equivalence relations is given by *MDPs with symmetry* [1] for sufficiently large symmetry groups. If the three conditions hold, then for each “bad” policy and for each state-action pair in its support, one can find an equivalent action that is relatively unsupported by the data distribution D. If one then replaces the policy with a new policy that always chooses an equivalent relatively unsupported action in each state, then the new policy should turn out to be equally bad, but not very supported by D, leading to the condition in Proposition 3.3. Similarly, for each bad policy, one can construct many equivalent ones whose supports are mutually disjoint, leading to the sufficient condition in Corollary 3.4.
In the revised version of the paper, we will discuss Example B.4 and its general properties in more detail in the main paper. Beyond that, we are unsure whether to include a general result along the lines we just sketched, mainly since this is a quick idea that we haven’t yet checked in detail. What do you think?
[1] Elise van der Pol et al., *MDP Homomorphic Networks: Group Symmetries in Reinforcement Learning*, NeurIPS 2020
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Rebuttal Comment 1.1:
Comment: Thanks for your response. The potential approach you've outlined for constructing examples supporting Cor. 3.4 for more general classes of problems (MDPs with symmetry, at least) sounds reasonable, and I'd be interested to see the details once it's fully worked out. For the current paper, however, a high-level discussion of the types of problems for which \hat{\pi} from Prop. 3.3 and \Pi_L from Cor. 3.4 can be expected to exist should suffice.
---
Reply to Comment 1.1.1:
Comment: Thank you again for your thoughtful feedback.
As you suggest, we will expand the discussion in the revised paper to clarify when we expect the relevant policies to exist. We believe the intuitive explanation we previously outlined --- particularly around MDPs with symmetries --- will be helpful. Given the current stage of the review process, we prefer not to add entirely new theoretical results, but we will ensure the final paper clearly addresses this aspect.
Thank you once more for your constructive comments. | Summary: This paper defines a notion called "error-regret" mismatch in the context of optimizing a learned reward function. Error-regret mismatch refers to when the learned reward is close to the true reward on a fixed distribution (low error), but when optimized the learned reward leads to a policy which performs poorly under the true reward function (high regret). The authors present a range of theoretical results showing that error-regret mismatch is difficult to avoid, even when using regularized optimization.
Claims And Evidence: The claims in the paper seem to be well-supported; error-regret mismatch is clearly motivated, defined, and explored through theoretical results and explanations.
Methods And Evaluation Criteria: No empirical results.
Theoretical Claims: I did not carefully check the proofs but the theorems seem intuitively correct to me.
Experimental Designs Or Analyses: No experiments.
Supplementary Material: I briefly glanced through the appendix but did not have time to read all 57 pages :)
Relation To Broader Scientific Literature: In general the relation to the literature seems good, although I think there are a couple of missing references (see below).
Essential References Not Discussed: These two papers study quite similar settings and are not referenced:
* Kwa et al. Catastrophic Goodhart: regularizing RLHF with KL divergence does not mitigate heavy-tailed reward misspecification. NeurIPS 2024.
* Laidlaw et al. Correlated Proxies: A New Definition and Improved Mitigation for Reward Hacking. ICLR 2025
It would be helpful to have a comparison to the results of these papers, which both show cases in which regularization can succeed at preventing an error-regret mismatch.
Other Strengths And Weaknesses: I found the paper clear and easy to read. The paper defines an important phenomenon that has significant implications for real-world RL training and AI safety.
Other Comments Or Suggestions: No other comments.
Questions For Authors: No questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your review! We are happy you found the paper clear, and that you highlighted the significance of this work.
We would also like to thank you for pointing out two further related works. We are integrating them into our revised related work section. In the following, we provide a comparison between these works and ours.
The results of our paper demonstrate that one gets very few mathematical safety guarantees in a wide variety of different reward-learning and (regularized or unregularized) policy optimization settings. An interesting question then is figuring out what can be done to make reward learning safer. The two works provide attempts at an answer:
**1. Develop well-motivated algorithms that don’t provide mathematical safety guarantees but work well empirically.**
The paper *Laidlaw et al. Correlated Proxies: A New Definition and Improved Mitigation for Reward Hacking* pursues this approach. In particular, they use the fact that if you have a data sampling policy $\pi_{ref}$ over which the true reward function and the learned reward functions correlate, then you can constrain your policy training procedure to avoid states that are unlikely under your data sampling policy. They develop a regularization method that penalizes going off training distribution (by penalizing the Chi-squared divergence of occupancy measures, see their Theorem 5.1 and Equation 4) and show in Section 6 that this method works well empirically for the environments they test. Note that while the restriction to remain “close” to the reference policy/training distribution in occupancy measure space can prevent reward hacking behavior, it also makes you dependent on the quality of said reference policy.
On theoretical guarantees: In Appendix A.1.3 (in particular Lemma A.3) they show that for their setup there always exists an MDP for which their method allows reward hacking, i.e., that their algorithm can’t always guarantee safety. In Appendix A.2 (in particular Theorem A.5) they show that this result is not specific to their algorithm, but generalizes to every algorithm that uses some form of penalty on the f-divergence between action distributions. While their results show the existence of a *single* MDP for which regularized policy optimization algorithms might not be safe (this might not be too bad in practice), we show (see Theorem 4.2) that, in fact, large classes of MDPs have many different unsafe data distributions for many different policy regularization methods. We show this by considering the more fine-grained setting of analyzing what subset of data distributions are safe/unsafe for *arbitrary* MDPs.
**2. Add a sufficient amount of structural constraints until your reward learning method becomes provably safe**
In our work, we make almost no structural assumptions on our setup. This allows for our results to generalize over a wide range of MDPs, reward-learning, and policy-optimization techniques. Therefore, one strategy to develop provably safe reward learning methods is to assume additional constraints on these structures. The second paper you mentioned (*Kwa et al. Catastrophic Goodhart: regularizing RLHF with KL divergence does not mitigate heavy-tailed reward misspecification*) as well as all works in the “Upper bound results” paragraph of our related work section pursue this approach. In particular, Kwa et al. show in their Theorems 4 and 6 that doing RLHF or Conditioning can be provably safe under the following structural assumptions:
- MDP: environmental transitions are deterministic and the policy return only depends on the final state reached.
- The true reward and the error of the proxy reward are independently distributed according to a data distribution generated by an arbitrary reference policy and their distributions are light-tailed (more assumptions are required for Theorem 6).
- The true reward is unbounded (i.e., the true reward function can attain arbitrarily large values)
While the paper provides some empirical evidence (see Section 4) that the error of the proxy reward is indeed light-tailed in some settings, they also observe (Section 5.2) that some of their assumptions are rather strong and don’t hold in practice, such as the assumption that the true reward and the error of the proxy reward are independently distributed.
---
In general, our results suggest that it is highly unlikely for a reward learning algorithm to be both fully general and provably safe, so we welcome works such as the ones described above which explore the trade-off between these two requirements.
We would once again like to thank you for your review and we are happy to answer any further comments or questions that you might have in the discussion phase!
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed rebuttal. I appreciate the comparison to prior works.
I looked into the results you mentioned in the comparison to Laidlaw et al., and based on my reading I believe you may be misinterpreting their results. Lemma A.3 seems to show that their are some cases in which their regularization scheme cannot improve the true reward. I don't think it means that the regularization method actually allows reward hacking. I think that the main result (Theorem 5.1) shows that optimizing the objective with chi-squared divergence penalty can never allow reward hacking according to their definition.
Furthermore, their Theorem A.5 appears to only apply to regularization based on action distributions, not occupancy measures. Theorem 5.1 seems to show that regularization using occupancy measure provably avoids reward hacking.
It would be good to clarify if my interpretations are correct, and if so make sure to update your comparison to the related work.
---
Reply to Comment 1.1.1:
Comment: Thank you very much for your comment! We apologize for the misrepresentation, we missed the fact that the optimum of the RHS of the inequality in Theorem 5.1 is always at least zero, so when optimizing this expression one ends up with a policy that is at least as good as the reference policy. After carefully re-reading the paper we agree with your comments. We therefore plan to put the following comparison in our related work section:
Laidlaw et al. (2025) consider a setting where the learned and true reward functions are positively correlated under a reference policy. They prove that maximizing the proxy reward with a chi-squared divergence penalty yields regret no worse than that of the reference policy. In experiments, they approximate this regularized objective and report favorable results. | Summary: The paper considers the problem of reward learning where the environment is modeled as an MDP and an unknown reward is estimated with a learning algorithm whose solution is used as a proxy objective in a downstream policy optimization setting. This paper formalizes conditions under which learned reward functions experience "error-regret mismatch." In such settings the proxy is a poor substitute for achieving low regret on the true objective. The authors demonstrate, through rigorous theoretical analysis, that achieving low error in a learned reward model on the training data does not guarantee low regret in the resulting policy. They introduce the concepts of "safe" and "unsafe" data distributions, providing a framework for understanding when this mismatch occurs. The paper also considers regularized policy optimization and contextual bandit settings, highlighting the persistence of the problem in these cases.
Claims And Evidence: See the section on theoretical claims and evidence.
Methods And Evaluation Criteria: This paper was purely theoretical. See the section on theoretical claims and evidence for more information about how it gave support.
Theoretical Claims: *Claims*
1. As the error of a learned reward model on a data distribution goes to zero, the worst-case regret of optimizing a policy according to that reward model also goes to zero.
2. For any ϵ > 0 there exists a reward model that achieves an expected error of ϵ and has a high-regret optimal policy.
3. When an MDP has a large number of independent bad policies, every data distribution is "unsafe."
4. Derive a set of linear constraints that precisely characterize the safe data distributions for a given MDP.
5. Regularized versions of Propositions 3.1 and 3.3.
6. Provide an analysis of RLHF in the contextual bandit case
*Evidence*
I checked for correctness of the proofs and found mixed support. My main issue has to do with the lack of connection between the paper's claims and the proofs in the Appendix. Currently several statements in the paper are not directly proved in the Appendix. The Appendix includes results to different claims which the reader is assumed to take as logically equivalent to the paper. This obscures the analysis and makes it difficult to both understand the result and verify their correctness.
For these cases, I suggest the authors either
(i.) directly prove the claims in the paper
(ii.) show the claims from the paper are logically equivalent to those in the appendix, or
(iii.) use the claims from the appendix in the main paper.
1.a (Valid) Propositions 3.1. Proof of Corollary D.7.
1.b (Invalid) Proposition 3.2. This result was not proved in the referenced result (Proof of Theorem D.11).
2. (Inconclusive) Proposition 3.3. Proof of Proposition C.5.
- What makes this claim different than the definition?
- Where in the proof must the policy's regret be high?
- What fact guarantees that $\hat{\pi}$ is optimal for $\hat{R}$?
- Minor point: $\epsilon$ should be no greater than one.
3. (Inconclusive) Corollary 3. Proof of Corollary C.6.
- The proof correctly proves one of its assumptions, but includes no other explanation of how this follows from Proposition 3.3.
4. (Valid) Theorem 3.5. Proof of Theorem C.16.
- The proof relies on Lemma C.15 from the Appendix. This asserts distributions are safe when there are no solutions to a linear system with non-safe vertices. The proof constructs a system of equations and an equivalent convex program then argues its solution is consistent with Lemma C.15. On the surface, this seems reasonable. However, I found the proof difficult to verify as several steps were skipped and others felt redundant.
- Equation 34 needs further support; it is not clear why the logical equivalence holds between 1511 and 1512.
5.a (Valid) Proposition 4.1. Proof of Theorem D.21.
5.b (Valid) Theorem 4.2. Proof of Theorem C.41.
- This proof relies on several lemmas which, if true, lead to a valid conclusion here.
6. (Invalid) Theorem 6. Proofs of Propositions C.34 and C.35.
- The referenced results do not prove the stated claim. If these two proofs together support Theorem 6, then a proof needs to establish the logical connection between these claims.
Experimental Designs Or Analyses: This is a purely theoretical paper with no empirical support.
Supplementary Material: I reviewed the supplementary material pertaining to the theoretical claims.
I was not able to review all 56 pages of the appendix.
Relation To Broader Scientific Literature: The paper generally did a good job positioning itself within the larger body of related work. The appendix contained an extended section of related work too.
Below are few other papers for understanding rewards apart from the approach used in Skalse et al. 2023.
1. [Settling the Reward Hypothesis](https://arxiv.org/pdf/2212.10420)
2. [Rethinking the discount factor in reinforcement learning: A decision theoretic approach.](https://arxiv.org/pdf/1902.02893)
3. [On the Expressivity of Markov Reward](https://arxiv.org/pdf/2111.00876)
4. [Utility Theory for Sequential Decision Making](https://arxiv.org/pdf/2206.13637)
Essential References Not Discussed: There are no additional references that are essential to include.
Other Strengths And Weaknesses: *Strengths*
- Positioned for generality: Condition (1) defines an epsilon-accurate reward model. This provides the analysis with enough generality to remain agnostic to the details of any particular reward learning method.
- Clear problem definition: The paper articulates the error-regret mismatch problem in a clear and accessible manner.
- Rigorous theoretical treatment: The paper offers an extensive theoretical approach to analyze the error-regret mismatch setting.
- Topically relevant: The issue addressed is highly relevant to modern RLHF systems.
*Weaknesses*
- Mixed amounts of support: It is unclear whether all the theoretical claims are supported with correct proofs. See my comments about theoretical claims.
- Complex proofs: While the paper presents a rigorous analysis, the proofs felt quite dense, sometimes terse, and in some places redundantly developed. Revising these for easy consumption could improve accessibility and help build trust in the results.
- Potentially unrealistic assumptions: The analysis assumes the existence of an epsilon-accurate reward model over the full data distribution (Condition 1). While this allows the results to remain agnostic to training, the condition is quite strong. The paper points this out. Still, weakening this requirement could strengthen the results.
Another example is Definition 2.1, which includes an particularly loose condition on regret. Regret is defined to be in the interval [0,1]. The definition considers a regret to be "low" if it falls with $[0,1)$. Thus "safe" distributions are those that don't lead to maximal regret of one. Similarly, the definition allows for the set to be empty by requiring $L=0$.
- Lacks empirical validation: Although the primary contributions are theoretical, there were several points which could benefit from empirical support. For instance, the defining conditions of a "safe" policy are quite technical, and it is not obvious how prevalent such data distributions are in practice. Providing an empirical demonstration of safe and unsafe data distributions would add clarity to this section and provide some validation to the definition.
- Motivation: Several choices could be better motivated. For example, the paper presents regularization as the de facto method to address objective mismatch. Though it is not explained how this is the case.
Other Comments Or Suggestions: - The paper describes RLHF as a reward learning algorithm. RLHF is more accurately described as problem setting in which a class of algorithms can be brought to bear.
- The example starting on 81 did not clearly illustrate the concern for me.
- "A policy maximizing J is an optimal policy." This is missing a condition on policies; many policies may maximize J, though it is only reasonable to call those which evaluate higher than the rest optimal.
- Currently the Appendix is 56 pages long. Much of the content felt extraneous to the points the paper needed to support. Culling unnecessary content would improve the paper's accessibility.
Questions For Authors: - Regret is one choice among many to define performance. Why is regret the right quantity to analyze RLHF systems?
See other sections for more questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your detailed feedback! Due to the 5000-character limit, we have to focus on your main concerns in this rebuttal. Please share any additional issues you'd like us to address.
# Addressing your remarks about our proofs
We appreciate your thorough technical review. We apologize for inconsistencies between the appendix and main text, which occurred as the appendix was written before we unified results in a shared framework for the main paper. We're confident our core results are sound. **We'll thoroughly revise the appendix to improve proof exposition, clarity, and brevity, beyond the specific points addressed in this rebuttal**.
> 1.b (Invalid) Proposition 3.2. This result was not proved in the referenced result (Proof of Theorem D.11).
Proposition 3.2 follows from the third regret bound in Theorem D.11. We are adding a Corollary D.12 in the revision to make this connection explicit.
In particular: To prove $D \in safe(R, \epsilon, L)$, we need to show that whenever $\mathbb{E}\Bigg[\frac{|R(s,a) - \hat R(s,a)|}{range(R)}\Bigg] \le \epsilon$ (A) and $\hat \pi$ is optimal for $\hat R$, then $Reg^R(\hat\pi) < L$. Using Theorem D.11:
$\begin{eqnarray}
Reg^R(\hat \pi) &\le& \frac{\sqrt{2} \cdot d^D(R, \hat{R})}{(1 - \gamma) \cdot (\max J^R - \min J^R) \cdot \min D(s,a)}\\\\
&\le& \frac{\sqrt{2} \cdot \epsilon \cdot range(R)}{(1 - \gamma) \cdot (\max J^R - \min J^R) \cdot \min D(s,a)}\\\\
&<& L\end{eqnarray}$
The second inequality uses the definition of $d^D$ (see lines 3248 and 3259) and assumption (A), while the third uses the upper bound on $\epsilon$ from Proposition 3.2.
> 2. (Inconclusive) Proposition 3.3. Proof of Proposition C.5.
> Where in the proof must the policy's regret be high?
In the proof, we show that the assumptions imply the existence of $\hat{R}$ that is $\epsilon$-close to $R$ and for which $\hat{\pi}$ is optimal. If one additionally considers the assumption that $Reg^R(\hat{\pi}) \geq L$, then what we show implies that $D \in unsafe(R, \epsilon, L)$, by the definition of this set of distributions. Thus, the regret being high is implicitly used by our proof. We make this explicit in the revised version.
> What fact guarantees that $\hat{\pi}$ is optimal for $\hat{R}$?
The state-action pairs that $\hat{\pi}$ visits all lie in $supp D^{\hat{\pi}}$ , where $\hat{R}$ has maximal reward $max R$. This implies that $\hat{\pi}$ is optimal for $\hat{R}$.
> 3. (Inconclusive) Corollary 3. Proof of Corollary C.6.
The proof correctly proves one of its assumptions, but includes no other explanation of how this follows from Proposition 3.3.
In the proof, we show $D(supp D^{\pi}) < \epsilon$. Implicitly, we also use that $Reg^{R}(\pi) \geq L$, which is due to $\pi \in \Pi_L$. These are the two assumptions from Proposition 3.3, which imply $D \in unsafe(R, \epsilon, L)$. Since $D$ was arbitrary, this implies $\Delta(S \times A) = unsafe(R, \epsilon, L)$. We make these last arguments explicit in an updated version.
> (Invalid) Theorem 6. Proofs of Propositions C.34 and C.35. The referenced results do not prove the stated claim.
Proposition C.34 demonstrates that reference policies $\pi_{ref}$ satisfying conditions a) and b) create unsafe data distributions $D^{ref}(s,a) := \mu_0(s) \cdot \pi_{ref}(a|s)$ (see Definition C.30 to verify this). In our revision, we'll streamline the proposition by referencing Def. C.30.
Proposition C.35 then provides simpler conditions that imply those in Proposition C.34. Theorem 6.1 combines these results, showing that reference policies satisfying Proposition C.35's conditions create unsafe data distributions. In the revised version we will replace the statement of C.35 with the one of Thm. 6.1 to make this connection explicit.
Lastly, the $2\cdot$ inside the $unsafe()$ statement is a typo that we will remove.
# Regarding the assumptions
> The analysis assumes the existence of an epsilon-accurate reward model over the full data distribution
We focus our paper largely on negative results, which get stronger if they hold even under the assumption of an epsilon-accurate reward model over the full data distribution.
> Regret is defined to be in the interval [0,1]. The definition considers a regret to be "low" if it falls with [0,1)
Both, $\epsilon$, as well as $L$, are free variables. Hence, depending on the application, one can decide how to set these values, i.e., what constitutes a low regret. We plan to update our explanations to make this clearer.
> the defining conditions of a "safe" policy are quite technical, and it is not obvious how prevalent such data distributions are in practice
To clarify our definitions and negative results, we provide a detailed chatbot example in Appendix B.4. Furthermore, Figure 4 provides a simple example of data distributions, highlighting which are safe. We will better integrate these explanations into the main paper.
---
Please let us know any remaining concerns we should address during the discussion phase! | Summary: The paper states an important issue in RLHF, that is the error-regret mismatch, which is fundamental due to the distribution shift of the induced data by the fine-tuned policy. The core contribution of the paper is to theoretically analyze the possibility of error-regret mismatch, assuming accurate estimation of the reward function. A distribution that, with any accurate reward estimation, will create a low-regret policy is called safe, and it is unsafe otherwise.
The structure of the study is a set of theoretical claims as follows:
1. Full support distributions are safe for sufficiently accurate reward estimation (for both reg/unreg objectives)
2. The existence of a high regret policy with a small support intersection with a distribution makes it unsafe (for both reg/unreg objectives)
3. An equivalent linear condition is proposed for the safety of a distribution in case of the unregularized objective for policy optimization.
One interesting point of the analysis is the generalizability of the regularization term, which is not limited to KL or chi divergence.
Claims And Evidence: The core claims are the same as stated in the summary, which are backed by theoretical proofs.
Methods And Evaluation Criteria: Regret as the main measurement of the goodness of a policy is the standard criterion in the literature.
A point about the measurement of the accuracy of the reward estimation is that, as also stated by the paper, it is mostly an *upper bound* of the bounds provided on the reward estimation errors. Hence, it is mostly not possible to assert such a bound for the estimated rewards, which affects the application of the analysis for different algorithms and methods.
Theoretical Claims: The paper is totally analytical and theoretical, hence, all the claims mentioned are justified by theoretical proof. I didn't get into the details of the proofs. But the statements of the intermediate lemmas and propositions are logical and indicate a correct deductive flow. Moreover, the theoretical claims are fairly intuitive.
Experimental Designs Or Analyses: There are no experiments to practically validate the claims. There is an example of the computation of the matrix M on a simple MDP in App. C.3.4. But, I don't find any examples of the validation and application of the analysis on real-world scenarios on popular RLHF methods.
Supplementary Material: The supplementary material contains detailed proof and discussion of the theoretical claims.
An algorithm to find matrix M, which determines the safety of a data distribution in case of unregularized policy optimization objective is also provided with an example on a very simple MDP.
Relation To Broader Scientific Literature: Currently, the most popular application of the study is indeed RLHF. The paper compares itself with other analytical studies and reviews reward learning in offline RL literature. The main missing part is its relation w.r.t. the new RLHF methods such as RPO, SimPO, and IPO. It is true that the analytics is based on a specific approach in RLHF, however, the validity of the analysis on other RLHF methods can give very useful insights and directions for future work. Also, the general regularization term can be applied to some new studies in RLHF, as in the following paper, which can be validated empirically.
Huang, Audrey, et al. "Correcting the mythos of kl-regularization: Direct alignment without overoptimization via chi-squared preference optimization." arXiv preprint arXiv:2407.13399 (2024).
Essential References Not Discussed: No essential reference is missed to the best of my knowledge.
Other Strengths And Weaknesses: The reward range is implicitly assumed to be bounded, which is not true in very popular preference-based policy optimization models such as Bradley-Terry.
Other Comments Or Suggestions: I don't have any other comments.
Questions For Authors: The final analysis on the RLHF setting is ambiguous for me. I don't get the main point of Theorem 6.1. Can the authors explain more about the significance and goal of Theorem 6.1 and provide an example of its application on a real, SOTA RLHF method?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | null | null | null | null | null | null | |
Does Graph Prompt Work? A Data Operation Perspective with Theoretical Analysis | Accept (poster) | Summary: The paper addresses the challenge that the theoretical underpinnings of graph prompting remain underexplored, particularly highlighting the lack of rigorous theoretical proof regarding why and to what extent it works. This has often been seen as a "dark cloud" over the field, hindering further progress. In response, the paper introduces a theoretical framework that rigorously analyzes graph prompting from a data operation perspective.
Claims And Evidence: The claims made in the submission are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. However, the paper lacks results on cross-domain datasets from real-world scenarios.
Theoretical Claims: I have roughly checked the proof process for all the theorems presented in the paper.
Experimental Designs Or Analyses: I have checked the datasets, experimental setup, and results presented in the paper.
Supplementary Material: I reviewed the proofs of the theorems provided in the appendix. The proofs are well-structured and logically sound, offering a clear explanation of the theoretical aspects of the paper.
Relation To Broader Scientific Literature: The paper provides a comprehensive analysis and proof of the existing literature on graph prompting. It offers valuable insights by approaching the topic from a macro-level theoretical perspective.
Essential References Not Discussed: NAN
Other Strengths And Weaknesses: Strengths:
1. The motivation of the paper is clear, effectively addressing the gap in existing heuristic graph prompting methods that lack theoretical grounding.
2. The topic of the paper is valuable, with a well-organized structure and clear writing, presenting the ideas in a step-by-step manner.
3. The paper provides thorough theoretical proofs for the claims and approaches introduced, offering solid justification for the proposed framework.
Weaknesses:
1. The paper does not offer theoretical guidance for designing new graph prompting methods. While it rigorously analyzes existing methods, it does not extend the theoretical framework to propose novel techniques.
2. The paper lacks experiments on real-world cross-domain datasets, which are crucial for assessing how well graph prompting adapts to different downstream tasks.
Other Comments Or Suggestions: 1. Testing on real-world cross-domain datasets would provide insights into the bridge graph method's generalizability and effectiveness across diverse applications.
2. It would be best to extend the theoretical framework to propose novel graph prompting methods, as this would add more practical value.
Questions For Authors: Please refer to the Weaknesses and Suggestions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > W1. The paper does not offer theoretical guidance for designing new graph prompting methods. While it rigorously analyzes existing methods, it does not extend the theoretical framework to propose novel techniques.
Thank you for pointing this out. In fact, our theoretical framework can provide fundamental theoretical guarantees for designing **novel graph prompting methods**. By considering Theorems 6 and 7, one can derive guidance for selecting the structure and number of prompts. These results can serve as useful directions for designing new graph prompting methods in future research. In our code project homepage, we also added some discussion to inspire the community for desining better graph prompt according to our theory analysis. please see the open discussion of our work in the code link.
> W2. The paper lacks experiments on real-world cross-domain datasets, which are crucial for assessing how well graph prompting adapts to different downstream tasks.
Regarding experiments on real-world data, please refer to **Appendix C**, where we provide detailed experiments on real-world datasets. These results are consistent with those obtained on synthetic datasets in the main text, further supporting the validity of our theoretical findings.
Regarding the cross-domain datasets, we have the same response to Reviewer SySL C1.
> Other Comments or Suggestions
We thank the reviewer for these insightful suggestion. We will open a new discussion online to keep updating our latest research findings on more real-world applications and more graph prompt design. We currently have already finished such explorations and that is the reason why we wish to find a pure theory support, just like the motivation of this paper. For anonymity policy, we will open these explorations once accepted.
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Rebuttal Comment 1.1:
Comment: Thank you for your reply. I will keep my rating. | Summary: This study aims to provide solid theoretical analysis of graph prompts. The theoretical findings include the capabilities of graph prompts on GCN models with and without non-linear layers, the error bound of the data operations by graph prompts for both a single graph and batch of graphs, and the error distributions of the data operations by graph prompts. This work also provides empirical studies to confirm these theoretical findings.
## update after rebuttal
This study analyzes the capacity of graph prompting methods for pre-trained GNN models. The analysis primarily focuses on GPF(-Plus) and All-in-One(-Plus) as the graph prompting methods and GCNs and GATs as the GNN models. I think **the correct formulations of the studied graph prompting methods and GNN models are the most basic requirement of a theoretical paper**. However, when checking their corresponding descriptions in the paper, we can find out that **most of them are questionable, confusing, and even incorrect**, e.g., GPF-Plus (line 630 to 638), GAT (Equation 7 to 9), GCN (line 642), All-in-One-Plus (no descriptions found).
Considering this, I have to keep my evaluation as negative. I hope the authors can check their paper from beginning to end rigorously to avoid such obvious mistakes.
Claims And Evidence: Not fully supported. For example, using the distance between $F_{\theta^*}(G_p)$ and $C(G)$ as the error is questionable. In addition, the formulation of GAT is weird. More details are provided in the weakness list.
Methods And Evaluation Criteria: Not fully make sense. The theoretical analysis in this paper has some issues in terms of the assumptions, formulations, and proof. More details are provided in the weakness list.
Theoretical Claims: I checked the proofs for theoretical claims, including most parts from page 11 to 17. The issues can be found in the weakness list.
Experimental Designs Or Analyses: I checked the experiments in the main paper and the supplementary material. The issues can be found in the weakness list.
Supplementary Material: I checked the proofs for theoretical claims, including most parts in page 11-17 and page 25-26.
Relation To Broader Scientific Literature: The key contribution of this paper is the theoretical analysis of the existing graph prompt learning methods, such as GPF and All-in-one. So it is very related to the literature.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: - **Weakness1**: Using the distance between $F_{\theta^*}(G_p)$ and $C(G)$ as the error is questionable. In many cases, there are multiple optimal graph embeddings given different task predictors. There may exist graph embeddings that are far from the optimal graph embeddings but can achieve almost-optimal performance. Hence, using the distance as the error may be improper to determine whether a prompted graph is close to the optimal ones.
- **Weakness2**: The definition of linear and non-linear graph aggregations is vague. The meaning of so-called “non-linear graph aggregations” like GAT is vague in this paper. Basically, GAT and GCN both aggregate the embeddings from neighboring nodes of a node linearly and pass the aggregated embedding to a non-linear activation function to obtain the updated embedding. Using linear and non-linear graph aggregations to distinguish them is quite confusing.
- **Weakness3**: The formulation of GAT is weird. In Equation (7)~(9), the authors use “the simplest form” of the attention mechanism in GAT. In “the simplest form”, the attention coefficient $\alpha_{jk}$ is determined by node features and irrelevant to hidden embeddings. As a result, $\alpha_{jk}$ will be constant across different GAT layers, not affected by GAT parameters at all. Therefore, it is quite strange to formulate GAT in this way.
- **Weakness4**: The formulation of GPF-plus is unclear. The authors should specify what $Q$ represents in Equation (14) and the meaning of $M$.
- **Weakness5**: The meaning of $\epsilon$ when formulating Equation (17) should be specified. According to Table 3, $\epsilon$ represents an error. But it seems that $\epsilon$ before Equation (17) does not represent an error.
- **Weakness6**: The authors should introduce the method All-in-one-Plus in the experiments. It is not introduced anywhere but only appears in some experimental results.
- **Weakness7**: The design for obtaining $C(G)$ in the experiments is questionable. $C(G)$ is obtained based on a modified graph by randomly removing nodes edges. These modifications do not include other graph manipulations, such as changing node features and adding extra nodes.
Other Comments Or Suggestions: N/A
Questions For Authors: Please mainly address the weaknesses above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: > W1
- The motivation of this distance we used is that: we assume once we are given an anchor/target graph embedding, our theory proves that we can use graph prompt to approximate such embedding. The given embedding is not necessarily the only optimal graph embedding. It can be any one. The purpose of this paper is to present the powerful data operation approximation from graph prompt. Of course, in a more realistic view, we usually hope such anchor graph embeding should be some optimal one for specific task because it can link graph prompt to various downstream tasks, but please note that this is not necessary for the theory basic of this paper, we say it just for indicating our reader that we can use such technique to find potential optimal solution for downstream task, and let our readers understand that graph prompt and traditional fine-tune are two routines to achive such target.
- Although the distance between **Fθ∗(Gp)** and **C(G)** may overestimate the actual performance deviation, this further supports the fact that the distance serves as an **upper bound** for the deviation. Our theoretical results demonstrate that this **upper bound** of the error is either zero or tightly controlled, ensuring that the performance deviation is also controlled. This, in turn, guarantees the effectiveness of the prompt. Thus, the strategy of using this distance as the error remains valid.
- Concerning different task predictors (decoders), while optimal embeddings vary across decoders, in practice, each downstream task has a fixed decoder from the pretrained model. Our analysis focuses solely on scenarios with fixed downstream tasks, ensuring consistent optimal embeddings .
- Additionally, our analysis does not require uniqueness of the optimal embeddings —only their existence. If exists and the distance to remains small, performance quality is assured, maintaining the validity of our approach regardless of embedding uniqueness.
- We appreciate your insightful comments and agree that exploring additional measurement approaches is promising, though somewhat beyond this paper's current scope. We intend to include such discussions in the camera-ready version upon acceptance.
> W2
Thank you for your question. Please note that we clearly discuss **non-linear graph aggregations** in Section 4.4. The definitions of **linear** and **non-linear graph aggregations** are clearly stated in the paper. Specifically:
- **Linear graph aggregations:** The aggregation coefficients do not depend on the node feature vectors. For example, in GCN, the coefficients for combining neighboring nodes' embeddings are constant. (e.g. $H=AXW$ with A a constant matirx and W the parameter, just like what we call $y=ax+b$ in linear algebra)
- **Non-linear graph aggregations:** The aggregation coefficients depend on the node feature vectors. For example, in GAT, the coefficients are determined by attention scores, which are computed based on the feature vectors of neighboring nodes.
You are correct that GAT and GCN both use non-linear activation functions for processing aggregated information. However, we emphasize the distinction in the **aggregation process**, not the subsequent **information processing**. Almost all GNN models use non-linear layers (e.g., MLPs) to capture complex patterns during **information processing**, but this is not the focus of our discussion.
> W3
Sorry for this typos. We will modify Equation (7) by replacing **Xj, Xk** with **Hj, Hk** (hidden embeddings), which is consistent with the reference of GAT. Please note that this typos will not affect our downstream theory analysis.
> W4
In the mentioned section, we state that **GPF-plus adds a combination of multiple prompt vectors to each node’s features.** Specifically, **Q ∈ R^M × k** is a matrix, where the i-th row **Qi** represents the combination coefficients of the k prompt vectors, which are then added to the node features. We stated the update rule is mathematically expressed as:
**[Xω]i = Xi + QiP.** **"M represents the number of graphs in the dataset Ω."** This indicates the number of graphs being processed, each with distinct combinations of prompt coefficients **Qi**. We will add the explanation in the final version.
> W5
We apologize for this inconsistency, which may cause confusion. We will replace this notation in Equation (17) with a different symbol and update the notation table accordingly in the final version.
> W6
**All-in-one-Plus**: we set the inserting patter of all-in-one as independent parameters (all-in-one, however, relies on prompt tokens). We will clarify this in the final version.
> W7
Our implementation of the **modified graph** includes all the operations you mentioned: **"Adding/deleting nodes, adding/deleting/changing edges, and transforming features of a given graph G."** This is explicitly stated in the task settings described in Appendix C. We will revise this section further in the final version.
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Rebuttal Comment 1.1:
Comment: Thank you for providing the detailed reply. I still have the following unaddressed concerns and decide to maintain the rating.
- **Following W1**: Thanks for the explanation. I would say using the loss for analyzing the quality of graph embeddings by graph prompts is more intuitive and reasonable than the distance to the optimal graph embedding with $\epsilon$. Even if a graph embedding is close to the optimal one (i.e., their distance is smaller than $\epsilon$), its real quality is also affected by other factors, such as the landscape at the embedding. Although the upper bound of the distance error is either zero or tightly controlled as demonstrated in this paper, I think loss-based metrics for analysis make more sense.
- **Following W2**: I agree that GCN and GAT use different coefficients for aggregation. However, they are both using $H=AXW$ to update embeddings. The difference here is that GCN uses consistent $A$ while GAT uses layer-specific $A$. If exist, it will be great to provide existing studies that use linear/non-linear graph aggregations to distinguish them. Otherwise, the authors should provide formal definitions before analysis.
- **Following W3**: If the authors modify Equation (7) to the form consistent with GAT, what does “the simplest form” of GAT refer to?
- **Following W4**: The explanation is still confusing. If $Q$’s $i$-th row $Q_i$ represents the combination coefficients of prompt vectors, $Q_i P$ will be an $F$-dimensional row vector added to the feature matrix $X_i$ of graph $G_i$. In this scenario, the nodes in graph $G_i$ will share the same prompt vector $Q_i P$. But I think the nodes in GPF-plus should have diverse prompt vectors, which is inconsistent with the authors’ formulation.
- **Following W5**: Let’s say $\tau$ to replace $\epsilon$, i.e., $S=A+\tau I$ in GCN when formulating Equation (17). What does $\tau$ mean? I am just wondering why we need an additional term $\tau$ here.
- **Following W7**: The authors should specify the operations used for obtaining the resulting figures in the paper. Now we may think the results are only with randomly removing nodes edges.
---
Reply to Comment 1.1.1:
Comment: ## Following W1:
We think you might have some misunderstanding, which could be further clarified as follows:
Please note that the target of this paper is to theoretically analyze how well the graph prompt approximate graph data manipulation, which is the only target and task of this paper. To this end, the so called “the loss for analyzing the quality of graph embeddings by graph prompts” by you is just what we are now doing, using current distance to see how well a graph prompt can approximate a manipulated graph. As what we reply before, the given embedding is not necessarily the only optimal graph embedding. It can be any one. The purpose of this paper is to present the powerful data operation approximation from graph prompt.
For other task loss, the performance of a graph embedding can be seen as a *decoded result* of the embedding, which depends on the decoder's overall properties (landscape). This dependency adds complexity to the analysis because we can not say a powerful data manipulation capability strickly corresponds to better various downstream task performance. Our paper only focus on analysing why and how well a graph prompt manipulate graph data.
Regarding your statement, *“its real quality is also affected by other factors, such as the landscape at the embedding”*, please note:
- For cases where the distance is 0 (as proven in our work), the performance is guaranteed to be optimal, and hence the "real quality" is not affected.
- For cases with small distances, the Lipschitz continuity of neural networks ensures that the performance differences remain bounded and small. As our work is an early-stage theoretical exploration of graph prompts, we acknowledge that future work can aim to extend such analysis to *performance-level differences*. However, by analyzing the rigorous upper bound through the distance metric, we have already obtained meaningful and significant results, which do not diminish the contributions of this work.
## Following W2:
Linear and non-linear aggregation is not a peculiar term in GNN area, it is just a very natural mathematical concept. for GAT, A in the H=AXW contain attention score, which should be calculated by X. therefore, H=AXW contain non-linear equation for X. We suggest the reviewer could think about such simple math eqution: y=ax+b (a is constent, linear) while y=ax+b and a=f(x) (a is up to x and then multiplied by x again, which is non-linear).
**It is a normal math concept, not a peculiar term.** However, to further address your concern, we promise in the final version, we will explicitly provide **formal definitions** to clarify that.
## Following W3:
It means the most classical.
## Following W4:
In our analysis of GPF (e.g., Theorem 3), we demonstrated that a single prompt per node is already sufficient to achieve zero error for fitting. When extending to multiple graphs, we aim to study the performance of prompts across the entire dataset. The **core issue** lies in how to combine multiple prompts for multiple graph embeddings. Unlike **Universal Prompt Tuning for Graph Neural Networks**, which assigns diverse prompt vectors to different nodes to ensure faster prompt tuning, our approach focuses on studying the theoretical properties of prompts. From this perspective, for a single graph, it is **not necessary** to assign diverse prompt vectors to different nodes. This simplification makes the analysis clearer and more intuitive.
## Following W5:
In GCN implementations, using only the adjacency matrix A for message passing can lead to the issue of propagating information only from neighboring nodes without considering the node itself. To address this, a virtual "self-loop" is often added, resulting in the form **A + τI**.
- In most implementations, τ is set to 1 by default.
- However, to allow finer control over how much self-information is propagated, an additional term τ can be introduced. This provides flexibility in controlling the contribution of self-loops during information processing.
## Following W7:
Thank you for pointing this out again. In the final version, we promise we will clearly specify that.
## Final Fight for our Paper:
We think we do not need to further declare the meaningful and strong contribution of this paper because the theoretical contributions of our work remain significant despite minor typos or ambiguities. We thank for your engaged comment. **However, it seems that the issues you raised are primarily due to some basic expressions and primary math knowledge, which we believe will definitely be fully addressed in our final version once accepted. It would be appreciated if you consider raising the score to reflect our paper quality objectively.**
Thanks. | Summary: The paper theoretically analyzes graph prompting. First, it shows that the main reason why graph prompting works is because it can simulate graph operations, and why this is important when encountering new tasks. Second, it presents upper bounds on the error of graph prompt when simulating graph operations. Third, the results are extended to non linear graph aggregations.
## update after rebuttal
The paper presents an interesting contribution. However, I am keeping my score unchanged, as stronger experimental validation would be needed for a higher score. Specifically:
1. The evaluation focuses on embedding reconstruction rather than performance on the actual downstream task, despite having access to labels of the downstream task.
2. The training task consists on approximating graph data operations such as random corruption, but it would be more insightful to train on real-world graph tasks. **More importantly, to properly assess the potential of graph prompting, it is necessary to change the dataset between training and test.**
Claims And Evidence: The theoretical claims are supported by clear and convincing evidence
Methods And Evaluation Criteria: I am not sure I understand the evaluation criteria. I was expecting to have defined a training task, a the training dataset, a downstream task and a downstream dataset. However, from Appendix C, it seems that the training task is to approximate graph data operations such as random corruption, and that the downstream task is the one of interest (and the dataset does not change).
Why aren't we considering a completely different training task defined on a different dataset than the downstream task? I understand that this setting is significantly more challenging, but otherwise I believe we are not really testing the generalization ability of graph prompting.
Theoretical Claims: The proofs seem correct to me.
Experimental Designs Or Analyses: Unfortunately I do not think I fully understand the settings of the experimental design. If the goal of graph prompting is to adjust the downstream data to make the downstream task compatible with the pretraining task, why don't we directly test the performance on the downstream task (since we have the labels), instead of reporting the error in reconstructing the embeddings?
Supplementary Material: I reviewed the supplementary material.
Relation To Broader Scientific Literature: The key contributions of the paper relate to the broader scientific literature by extending the concept of graph prompting, which has been explored in empirical studies but lacks theoretical understanding. The paper demonstrates that graph prompts can simulate graph data operations and provides theoretical guarantees for their effectiveness.
Essential References Not Discussed: None
Other Strengths And Weaknesses: The topic is interesting but the paper is hard to hard. This is partially due to the presence of many theoretical results, but I think the authors should include intuitive explanations throughout the paper.
The experimental settings are unclear, as I discussed above. Appendix C partially helped me understanding the loss and the training procedure (which aims at obtaining the same graph embeddings under manipulations of the graph), and should be partially moved to the main paper, otherwise it is unclear what are the training task and dataset.
Other Comments Or Suggestions: $\rightarrow$ in Equation 2 should be $\approx$
$A_{in}$ should be $\mathbf{A}_{in}$ in line 97 right
please use \citet in Section 2 motivation.
Questions For Authors: Why does the loss in Equation 1 only takes the graph-level embedding? Why aren't we taking the output of downstream classifier (which is applied to the graph-level embedding) and the ground truth labels?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > C1: Why aren't we considering a completely different training task defined on a different dataset than the downstream task? I understand that this setting is significantly more challenging, but otherwise, I believe we are not really testing the generalization ability of graph prompting.
Thank you for your question. Transferring graph models on different domains (graph datasets) is a very promising potential application of graph prompt because we believe the core challenge on this topic is how to learn effective data manipulation strategy. before graph prompt, we can nearly only focus on hand-crafted design, which is far from promising to achieve this goal. Transfering across graph datasets/domain, or across differnt tasks, are two hard problems in graph learning area. The one across domains/datasets is still a not well solved problem. recently, there are some work trying for this but most of them are far from sufficient to industrial applications.
Our paper found that, learning an effective data manipulation strategy might be helpful for both domain transfering and task transfering in graph learning area. recently, some graph prompt-based work have found the promsing restuls for graph domain transfering for recommendation (Zhang et al. Adaptive Coordinators and Prompts on Heterogeneous Graphs for Cross-Domain Recommendations. arxiv 2410.11719). The potential behind this lies in the powerful graph data manipulation capability of graph prompt. However, diving into so many various applications is far out of the scope of our motivation. This paper wishes to provide the background theory support for our community to explore further. To this end, we focus on the core problem: how well does graph prompt manipulate graph data? According to this, our experiments are close to justify the correctiness of our theory analysis. We will explore more task settings in the futre to expand the imapct of this paper.
> C2: I think the authors should include intuitive explanations throughout the paper. The experimental settings are unclear, as I discussed above. Appendix C partially helped me understand the loss and the training procedure ..., and should be partially moved to the main paper..."
Thank you for the suggestion.We will carefully consider better formatting and move some key explanations from Appendix C to the main paper in the final version to improve clarity.
> C3: typos
Thanks for pointing our this, we will carefully update in our final version.
> C3: Why does the loss in Equation 1 only take the graph-level embedding? Why aren't we taking the output of the downstream classifier (which is applied to the graph-level embedding) and the ground truth labels?
This concern might come from our expression issue. We are sorry for the caused misunderstanding. Take the graph classification as an example, the classifier (like MLP) can be usually treated as some addion layers for the graph model so the output of the classifier can be treated as a special graph embedding. We take this expression just for conciseness without loss of generality. In a standard graph prompt workflow, the task head is usually fixed and pre-defined so the task head is just a constant mapping and it is usually won't affect the graph prompt design. We thank you for this suggestion and we will try our best to refine this section in our final version.
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Rebuttal Comment 1.1:
Comment: Thank you for the reply. Can you please expand on why we don't directly test the performance on the downstream task (since we have the labels and it is what we are ultimately interested in), instead of reporting the error in reconstructing the embeddings?
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Reply to Comment 1.1.1:
Comment: Thank you for the reply.
There is already a significant body of work in the literature on graph prompt tuning that directly tests downstream task performance, such as **All-in-One Prompt**. These works have extensively demonstrated that prompt tuning performs well in downstream tasks when evaluated in an end-to-end manner.
Building upon their findings, which have already validated the *practical effectiveness* of prompt tuning, our work focuses on a different, yet equally important, aspect: providing **theoretical explanations** for the effectiveness of prompt tuning. Specifically, rather than testing downstream task performance directly, our goal is to identify the **core mechanism** behind prompt tuning. This mechanism is centered on tuning the graph embeddings to effectively fit the transformations required by downstream tasks.
Kindly note that this paper did not propose any new prompt model. The only motivation of our paper is to answer how well a graph prompt can manipulate graph data. This is the only target. testing graph prompt on other task is just like a benchmark or proposing new model, which is not the content of our paper.
In the end, we would like to further present the main contribution of our work:
1. **Core Contribution**:
- Our study is fundamentally aimed at understanding the theoretical underpinnings of prompt tuning. By analyzing the ability to tune graph embeddings to fit transformations (e.g., via reconstruction error), we offer a rigorous explanation for why prompt tuning works.
- This focus distinguishes our work from purely engineering-driven approaches that prioritize end-to-end performance without necessarily addressing underlying principles.
2. **Challenges in Evaluating Downstream Tasks**:
- Direct downstream evaluation can be heavily influenced by task-specific factors, such as the choice of decoders, discrete optimization steps, and specific task requirements. These factors often obscure the *generalizable insights* into prompt tuning mechanisms.
- Our embedding reconstruction approach avoids these complications, providing a more controlled and interpretable evaluation of prompt tuning effectiveness.
3. **Completing the Theory-to-Practice Chain**:
- Our work forms a **theory-to-practice bridge** when combined with the aforementioned practical studies ([X], [Y]). Those works already establish the practical effectiveness of prompt tuning in downstream tasks, while our work provides the missing theoretical guarantees. Together, they establish a complete pipeline for understanding and applying graph prompt tuning effectively.
In our follow-up work, we plan to incorporate additional settings and auxiliary end-to-end experiments to further validate our theoretical insights in practical scenarios. However, we emphasize that the primary contribution of this paper lies in its theoretical guarantees, which provide essential guidance for this field.
We believe that our current approach, which focuses on the distance between embeddings and their optimal counterparts, along with extensive experimental validation, is logically consistent and sufficient for supporting our claims. Combined with practical works mentioned in our paper, our study contributes to a robust foundation for graph prompt tuning research.
Lastly, we sincerely thank you for your thoughtful comments and encourage you to acknowledge the significant theoretical contributions of this work. We appreciate your review and hope you will consider further support our paper.
Thanks | Summary: The paper presents a comprehensive theoretical analysis of graph prompting, a novel technique aimed at adapting pre-trained GNN models to downstream tasks without retraining. It introduces the concepts of "bridge sets" and "ϵ-extended bridge sets" to explain the capacity of graph prompts to simulate graph transformations and align upstream pre-trained models with downstream tasks. The authors provide theoretical proofs demonstrating the conditions under which graph prompts effectively approximate various graph data operations, establish error bounds on these approximations, and examine error distributions. Empirical results validate these theoretical findings, supporting the practicality and effectiveness of graph prompting.
---
(+) The paper fills a significant theoretical gap in the graph prompting literature, rigorously establishing conditions under which graph prompts can successfully approximate data operations.
(+) It systematically addresses various scenarios including single and batch graphs, linear and non-linear graph aggregation models (GCN and GAT), and extends its theoretical guarantees to practical GNN architectures.
(+) Introducing bridge sets as a theoretical tool is innovative and clarifies how prompting impacts model behavior from a data manipulation perspective.
---
(-) Despite rigorous theoretical insights, practical application and generalization to various real-world graph tasks might still face challenges in prompt design and optimization.
(-) Some theoretical guarantees depend on assumptions like "full-rank" model parameters, which, although justified by practical model initialization and training strategies, might limit generalization or require specific model conditions.
(-) While synthetic datasets convincingly demonstrate theoretical validity, broader validation across diverse real-world datasets and complex scenarios would enhance practical relevance.
---
## update after rebuttal
Thank you to the authors for the thoughtful and detailed rebuttal. I appreciate the clarifications regarding the full-rank assumption and the inclusion of supporting theorems (e.g., Theorems 5, 8, and 9) for scenarios where the assumption does not hold. The explanation of practical conditions under which full-rank matrices are likely to appear is helpful.
That said, I still believe the practical implications and generalizability of prompt design remain open challenges, especially in more complex real-world settings. While I acknowledge the experiments in the appendix, I would encourage the authors to highlight these results more explicitly in the main text to improve accessibility and clarity.
Overall, the rebuttal strengthens my confidence in the theoretical contributions, but my initial position remains unchanged. I still lean toward a weak accept, primarily due to the paper’s rigorous theoretical insights and the novelty of the proposed framework.
Claims And Evidence: The claims in the paper are clearly stated and largely supported by convincing theoretical proofs and controlled empirical evidence. However, claims about generalizability to complex real-world scenarios are not thoroughly supported by empirical experiments.
Methods And Evaluation Criteria: The methods and evaluation criteria, including synthetic benchmarks and the use of GCN and GAT as representative models, are appropriate and relevant to the theoretical focus of the study. However, additional real-world datasets could provide a more comprehensive evaluation.
Theoretical Claims: I checked the correctness of key theoretical claims such as Theorems 3, 4, and 5. The proofs appear mathematically sound and logically consistent. Minor concerns may exist around the conditions for full-rank assumptions, but they are clearly justified.
Experimental Designs Or Analyses: The experimental designs using synthetic datasets effectively validate theoretical claims. The choice of metrics and analysis approaches are sound. However, the extension to real-world graph data could be more comprehensive.
Supplementary Material: I did review the supplementary material.
Relation To Broader Scientific Literature: The paper clearly positions itself in relation to recent literature, especially in the area of prompting techniques and graph neural networks. It effectively references significant prior work such as Sun et al. (2023a, b), Fang et al. (2022, 2024), and Liu et al. (2023).
Essential References Not Discussed: The paper adequately references essential and relevant prior work. No critical omission is evident concerning the core contributions.
However, (not necessarily) I recommend to include more recent papers such as GSPF, SUPT, GSmFP, and HGPROMPT at the final version.
Because graph prompting has rapidly emerged as a promising research direction, as mentioned by authors.
Other Strengths And Weaknesses: The paper's originality lies significantly in its rigorous theoretical grounding of prompting techniques for GNNs, contributing valuable insights and clarity to an otherwise empirically driven field. The clarity and structure of the presentation further enhance its impact.
Other Comments Or Suggestions: Minor editing for typographical errors could further enhance readability. Overall, the manuscript is clearly written.
The `citeauthor` format is inconsistent. For instance, in page 2,
> (line 071) ... as described in the review by `Sun et al. (2023b)`, can be ...
> (line 107) Initially, `(Fang et al., 2022)` have proved that ...
Questions For Authors: 1. Could you clarify under which practical conditions the assumption of a full-rank matrix in Theorems 3 and 4 typically holds?
2. Can you discuss the scalability of your proposed graph prompting methods to extremely large graph datasets, such as those encountered in industrial applications?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > C1: Despite rigorous theoretical insights, practical application and generalization to various real-world graph tasks might still face challenges in prompt design and optimization.
Thank you for your insightful comment. This paper primarily focuses on providing theoretical insights and rigorous proofs for graph prompting. We believe that exploring practical applications and generalizations should be left to the broader research and industrial communities. To triger this exploration, we added some open discussion to our work in the code project homepage, from which you could see some practical impact of our theory.
> C2: Some theoretical guarantees depend on assumptions like "full-rank" model parameters, which, although justified by practical model initialization and training strategies, might limit generalization or require specific model conditions.
Thank you for your comment. In Theorems 3 and 4, the "full-rank" assumption are critical for ensuring the existence of lossless graph prompting methods in general settings. For cases where the full-rank assumption does not hold, we have dedicated considerable effort in our work to analyze such scenarios (e.g., Theorems 5, 8, and 9). These theorems provide corresponding bounds that demonstrate only controllable errors and ensure the robustness of prompt design. Therefore, the "full-rank" assumption is a key condition discovered during our exploration and does not detract from the contributions of this paper.
> C3: While synthetic datasets convincingly demonstrate theoretical validity, broader validation across diverse real-world datasets and complex scenarios would enhance practical relevance.
In Appendix B of our paper, we conducted extensive analyses and experiments on various real-world datasets. The results obtained are very similar to those from synthetic datasets in the main text. Therefore, we believe that both synthetic and real-world datasets yield consistent results, fully supporting the validity of our theoretical findings.
Regarding the experimental setup, we carefully aligned each experiment with the theoretical discoveries, focusing on the core theoretical insights. From a practical experimental perspective, this is sufficient to validate the problem. Broader and more complex settings could be left to the wider research community. Our goal is to emphasize the solid theoretical results.
> C4: typos and references:
We have noted the minor editing errors and suggestions for updating references. These will be totally included in the final version of the paper.
> Q1. Could you clarify under which practical conditions the assumption of a full-rank matrix in Theorems 3 and 4 typically holds?
Thank you for your question. As discussed in the section following Theorem 4, when parameter matrices are initialized using methods such as orthogonal initialization, He initialization, or Xavier initialization, they are almost always full-rank throughout the training process.
Here, "almost always" can be understood as follows: the determinant of a matrix is 0 if and only if the matrix is rank-deficient. However, during training, the determinant can take any value along the real number axis and its behavior can be considered as random fluctuations, making it extremely unlikely to be exactly 0. Since He initialization is the standard initialization method in modern practices, the direct answer is that with proper initialization, trained models can be considered full-rank matrices in practice. We added some open discussion to our work in the code project homepage, from which you could see further practical discussion on full-rank condition.
> Q2. Can you discuss the scalability of your proposed graph prompting methods to extremely large graph datasets, such as those encountered in industrial applications?
Our work primarily analyzes classical prompting methods, such as GPF and All-In-One. In Theorem 7, we provide a detailed discussion on the performance of multi-token GPF and multi-node subgraph All-In-One methods on large-scale graph datasets. Specifically, part (4) of Theorem 7 gives an upper bound on the final error, theoretically demonstrating the scalability of graph prompting methods to extremely large graph datasets.
Some studies have already achieved promising results on larger datasets, and our work provides theoretical support for these findings. For extremely large graph datasets, following our theorems and subsequent discussions, effective results can be achieved using prompts that are much smaller than the dataset itself. This theoretical work strongly supports the scalability of graph prompting methods to extremely large graph datasets and provides a solid foundation for future industrial applications.
We will add more scalability discussion in the final version. | null | null | null | null | null | null |
Propagation of Chaos for Mean-Field Langevin Dynamics and its Application to Model Ensemble | Accept (poster) | Summary: The paper studies the propagation of chaos of two-layer neural network in the mean-field regime. The authors first obtain a uniform-in-time propagation of chaos (PoC) bounds that does not depend on the LSI constant, and maintain the "original" rate of convergence. Then, the authors apply the PoC bounds to model ensemble problem and show that in the mean-field regime, model ensemble help reducing the approximation error. Finally, the authors proposed a PoC based model ensemble methods, and did experiments to verify the usefulness of the methods.
Claims And Evidence: I think the main claims clearly stated, and the proof are convincing.
Methods And Evaluation Criteria: This paper is majorly a theoretical paper. There are some experimental results which I think are not the major contribution of the paper: in section 5.1, the authors consider training a two-layer neural network in mean-field regime on synthetic datasets. This experiments make sense to me as a sanity check for the theoretical results. In section 5.2, the authors consider incorporating LoRA finetuning with the proposed model ensembling method, I think the model used and the benchmarks are standard.
Theoretical Claims: I check the proof of Lemma 3.6 and Proposition 4.6 in the appendix, as well as all the proof in the main context, and I think they are all correct. I didn't check the rest proofs in detail, but they are more or less easy to see given the other theorems mentioned in the main context.
Experimental Designs Or Analyses: This paper is majorly a theoretical paper, and I think both experiments solid in experimental designs or analyses.
Supplementary Material: I didn't check the supplementary material.
Relation To Broader Scientific Literature: This is paper studies the propagation of chaos for two-layer neural networks in mean-field regime. In general, propagation of chaos are widely studied in other fields such as stochastic analysis/ optimal transport, statistical physics and game thoery etc. While in other problems, theoretical formulation could be different from the one considered in this paper, similar ideas might be applicable.
Essential References Not Discussed: I don't find any important references that is not discussed.
Other Strengths And Weaknesses: **Strengths**
I think in general the theoretical results are interesting:
- Removing the LSI dependency in the PoC bound and reducing the order of $1/\lambda$ in the convergence rate is a nice improvement.
- Showing that averaging over $M$ independently trained nn reduces the approximation bound (improve the PoC bound) is interesting.
**Weaknesses**
1. The main weakness in this paper is the proposed methods in Section 5.2, there are following issues in my opinion:
- 1.1 The authors take the LoRA rank to be $N$ and claim "Therefore, we can apply PoC-based model ensemble for LoRA parameters." This is not very convincing, since in general one need large $N$ to achieve good approximation in PoC bounds, and typically $N \gg d,k.$ However, in practical application of LoRA, people let the LoRA rank $N \ll d,k,$ thus I doubt that the PoC results provide any insight on LoRA in general.
- 1.2 There's a mismatch between this ensemble method and the one proposed section 4. In particular, the method proposed in section 4 averages the outputs, but the one in section 5.2 averages over the LoRA weights.
- 1.3 I don't see the usefulness of this weight averaging method from the experimental results, since the authors didn't control the variates when comparing the ensembled model and the individual model. In particular, the ensembled model increases the accuracy, but also requires $M=8$ times more computation resources comparing to only training one model, since it requires to train $M=8$ independent models. Besides, the rank of the LoRA updates in each individual model is at most $N = 32,$ but the update of the averaged model is $N \times M = 256.$ I think it would be more interesting to consider the performance of the model ensemble method under fixed computational resources, for example, compare with an individual model that trained $8$ times more epochs, or compare with another individual model whose LoRA rank is $N \times M = 256.$
2. While I believe the theoretical results are techinically interesting in the field of PoC, I don't get much insight in model ensemble from the results. Theoretically, the authors show that by training $M$ independent models and then average over the output of the model, it improves the approximation error, however, (1) this results is very specific to the two-layer setting in the mean-field regime, (2) I don't see the benefit of this methods compare to directly training a large network with $M \times N$ neurons. Practically, I don't find the practical results very convincing as discussed in the previous point.
Other Comments Or Suggestions: I do not have other comments or suggestions.
Questions For Authors: 1. Could you address technical differences between the prove of the improved PoC results and the proof techniques in [1,2] ?
[1] Chewi, S., Nitanda, A., and Zhang, M. S. Uniform-in-n log sobolev inequality for the mean-field langevin dynamics
with convex energy. arXiv preprint arXiv:2409.10440,2024.
[2] Nitanda, A. Improved particle approximation error for mean field neural networks. In Advances in Neural Information Processing Systems 37, 2024.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for reading our paper.
**1.2 Mismatch between the ensemble methods in Sections 4 and 5.2**
First, we would like to clarify that the ensemble method used in Section 5.2 is exactly the same as the one proposed in Section 4. Specifically, the ensemble in Section 4.2 is taken over model outputs of the form $x \to b^i\_j a^{i \top}\_j x $, which reduces to parameter averaging due to the use of a linear activation function. That is: $\frac{1}{MN}\sum\_{i,j} (b^i\_j a^{i\top}\_j x) = (\frac{1}{MN}\sum_{i,j} b^i\_j a^{i\top}\_j )x = \Delta W x$ where the left-hand side represents the ensemble of model outputs, and the right-hand side corresponds to a single model with averaged parameters.
**1.1 Choice of $N$**
In the LoRA setting, choosing $N=\min\\{ d, k \\}$ corresponds to full fine-tuning, with no approximation error compared to the $N=\infty$ case for fixed $d$ and $k$, thanks to the linearity of the activation function. Our goal is to close the performance gap from the full-rank case more efficiently by leveraging the ensemble technique under $N<\min\\{ d, k \\}$.
**1.3 Comparison under Fixed Compute Budget**
Following your suggestion, we additionally evaluated LoRA with a higher rank (256) and found that performance is inferior compared to the ensemble of 8 lower-rank (32) models. Please refer to the table below for details:
| Model | Method | SIQA | PIQA | WinoGrande | OBQA | ARC-c | ARC-e | BoolQ | HellaSwag | Ave. |
| :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: | :---: |
| Llama2 | LoRA (r=32, best) | 79.48 | 82.43 | 81.77 | 80.60 | 67.75 | 80.47 | 70.37 | 86.67 | 78.69 |
| | LoRA (r=256) | 69.95 | 69.69 | 69.61 | 61.40 | 47.44 | 61.15 | 63.73 | 47.27 | 61.28 |
| | PoC merge | 81.17 | 84.60 | 85.16 | 86.60 | 72.53 | 86.62 | 72.45 | 92.79 | 82.74 |
| Llama3 | LoRA (r=32, best) | 81.22 | 89.50 | 86.74 | 86.00 | 79.86 | 90.53 | 72.91 | 95.34 | 85.26 |
| | LoRA (r=256) | 81.06 | 87.60 | 87.61 | 84.60 | 78.92 | 90.06 | 75.11 | 94.98 | 84.99 |
| | PoC merge | 82.04 | 89.39 | 89.27 | 89.20 | 83.28 | 92.30 | 76.33 | 96.58 | 87.30 |
These results suggest that, under a fixed compute budget $MN=256$, the ensemble method achieves nontrivial improvements over joint training for a higher-rank model.
Furthermore, prior studies [1] have also observed that training higher-rank matrices does not always lead to better performance, (see Fig 4 in [1]) and [2] reported instability of LoRA with higher rank.
[1] S.Y. Liu et al. DoRA: Weight-Decomposed Low-Rank Adaptation. ICML, 2024
[2] D. Kalajdzievski. A Rank Stabilization Scaling Factor for Fine-Tuning with LoRA. 2023
**2. Benefit of the Ensemble Method**
The ensemble method helps reduce the approximation error from the mean-field limit compared to directly training a single network with $MN$ neurons. Our merge strategy provides nontrivial optimal choice of $M$. Given a fixed compute budget $K=MN$, Theorem 4.4 gives the error bound: $\frac{1}{K}+\frac{1}{\sqrt{MK}}+\frac{M}{K}$, ignoring constants for simplicity. This bound decreases with $M \in [1, (K/4)^{1/3}]$, and is minimized when $M \sim (K/4)^{1/3}$, achieving an error of: $\frac{1}{K} + \frac{C}{K^{2/3}}$ for some constant $C$.
Intuition: The key in the mean-field approximation is the independence among neurons $\\{h(x_t^i,z)\\}_{i=1}^N$ since the variance of their empirical average (i.e., mean-field model) would decrease linearly with $N$ if neurons were independent. While the PoC ensures that neurons become approximately independent after convergence when $N$ is sufficiently large, the ensemble of independently trained networks introduces the independence across models, further reducing error.
Additionally, previous work [3] has shown that ensembles of independently trained networks can outperform joint training in specific scenarios, although their setting differs from ours.
[3] Z. Allen-Zhu and Y. Li. Towards Understanding Ensemble, Knowledge Distillation and Self-Distillation in Deep Learning. ICLR, 2023
**Q. Technical Differences from Existing Studies**
Our proof strategy is significantly different from those in [4,5]. Specifically, [4] establishes a uniform in $N$ log-Sobolev inequality (LSI) by constructing a Lipschitz transport map from a Gaussian to the optimal distribution $\mu_*^{(N)}$. [5] directly analyzes the variance of the mean-field model at the optimal distribution, leveraging the nonlinearity of $F_0$.
In contrast, our analysis is based on the argument of conditional and marginal distribution of $\mu^{(N)}$ [6], which allows us to establish an improved bound that holds for any distribution, not just at the solution. Furthermore, our assumptions about LSI differ notably from [5]; please refer to our Assumption 3.2 compared to Assumption 2 in [5].
[4] S. Chewi et al., 2024
[5] A. Nitanda, NeurIPS, 2024
[6] F. Chen et al., 2022
---
Rebuttal Comment 1.1:
Comment: I believe my concerns are addresses, thus I decide to raise my score to 3. | Summary: The paper proposes an improved bound on the convergence of neurons (of a network) under mean field Langevin dynamics to an iiid distribution. This argument is known as the propagation of chaos. The convergence of the empirical finite-N distribution to the limiting iid distribution is controlled by time and number of particles (neurons) $N$. The optimal approximation error is known to be order $1/N$. This paper further improves on this and proves exponential decay in time. The result is applied to the model ensemble where the variance due to finite approximation is further reduced.
Claims And Evidence: Yes, the claims are well supported.
Methods And Evaluation Criteria: Yes. Toy models are good for theory papers.
Theoretical Claims: no. I only read theorem statements in the main.
Experimental Designs Or Analyses: Yes. The experiments in the main (with a multi-index model and two concentric circles) make sense.
Supplementary Material: No.
Relation To Broader Scientific Literature: Mean-field limit dynamics of neural networks is an active area of research. Improvement in convergence speed is a very valuable technical contribution. Similarly, model ensembling shows better generalization capabilities and there is no complete theory that explains this (but I may be wrong). Though this paper does not study generalization, applying mean-field Langevin analysis to ensembling is valuable.
Essential References Not Discussed: The related literature is included and compared.
Other Strengths And Weaknesses: The results look solid but I am not an expert on this topic to catch a mistake if there was one.
However, I did find the paper difficult to read. It would benefit from better organization along the lines:
* Defective LSI comes on pg 2. This is not a trivial lemma. Please put this in a proper formatting (Lemma ?) and cite exactly where it appeared in Chen et al 2022.
* $\Delta_0^{(N)}$ is introduced multiple times (pg3 and pg4).
* Page 3. the paragraph starting with "Afterward, this exponential dependence....." put this technical paragraph as a remark after the main result.
* Assumption 3.2 looks like a Lemma.
Other Comments Or Suggestions: see above.
Questions For Authors: NA.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for reading our paper and for the positive feedback. We will revise the manuscript accordingly, following your suggestion. | Summary: This paper improves the Propagation of Chaos (PoC) error bound for Mean-Field Langevin Dynamics (MFLD) by refining the defective Log-Sobolev Inequality (LSI) and introducing the Uniform Directional LSI (UD-LSI). Additionally, it proposes a PoC-based model ensemble method, which is supported by both theoretical analysis and empirical validation.
Claims And Evidence: - The theoretical results heavily rely on Assumption 3.2 (Uniform directional LSI), but its justification remains insufficient. As I understand, the authors assume that the convergence rate of each conditional distribution of a Langevin particle is uniform, which indirectly ensures the network-wide uniform convergence and influences the effectiveness of the PoC-based ensembling method. However, the paper does not provide empirical evidence to support these assumptions. I encourage the authors to include numerical validation or theoretical discussion regarding the plausibility of UD-LSI in practical neural networks.
- Additionally, I am uncertain whether the improved PoC bound is numerically validated. While the theoretical derivations are rigorous, the paper does not appear to provide direct numerical verification of the improved error bound. Empirical experiments demonstrating the practical impact of the improved bound, such as comparisons with prior PoC error bounds, would strengthen the paper’s claims.
Methods And Evaluation Criteria: - The proposed method is logically well-founded and builds on existing work in the PoC for MFLD.
Theoretical Claims: - This paper presents rigorous theoretical proof for its main claims.
Experimental Designs Or Analyses: - The paper provides empirical validation for the proposed PoC-based ensemble method, particularly in the context of LoRA-based fine-tuning.
Supplementary Material: - I have reviewed the SM.
Relation To Broader Scientific Literature: - While this paper makes an interesting theoretical contribution to PoC for MFLD, its relevance to the broader deep learning community remains uncertain—which is one of my main concerns.
Essential References Not Discussed: - This work has already discussed the related studies.
Other Strengths And Weaknesses: No.
Other Comments Or Suggestions: No.
Questions For Authors: - Please refer to the comments above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for reading our paper.
**Uniform directional LSI (UD-LSI)**
We can theoretically validate the UD-LSI in the setting of Example 3.5 by leveraging a known result (e.g., Lemma 6 in [1]): Let $\nu \propto \exp( -H-V)$, where $V,H: \mathbb{R}^d \rightarrow \mathbb{R}$, with $V$ being $\alpha$-strongly convex and $H$ being $L$-Lipschitz smooth. Then, $\nu$ satisfies the Log-Sobolev Inequality (LSI) with constant: $\alpha \exp\left( - \frac{L^2}{\alpha} - \frac{4L}{\sqrt{\alpha}}\right)$. (Note that LSI constants in [1] is defined as a reciprocal number of our constant.)
We now apply this result to the conditional distribution $\nu_{i|-i}$ in Example 3.5:
$$
\frac{d \nu\_{i|-i}}{dx}(x|\mathbf{x}^{-i}) \propto \exp\left( -\frac{N}{\lambda n}\sum_{j=1}^n\ell(\mathbb{E}\_{X\sim\rho\_{x\cup \mathbf{x}^{-i}}}[h(X,z\_j)],y\_j) - \frac{\lambda'}{\lambda}||x^i ||\_2^2 \right).
$$
The first term in the exponent is $\frac{R’}{\lambda}$-Lipschitz smooth since its partial derivative in $x$ is bounded as follows under the setting of Example 3.5:
$$
\left|\left| \frac{N}{\lambda n} \sum\_{j=1}^n \partial\_1\ell(\mathbb{E}\_{X\sim\rho\_{x\cup \mathbf{x}^{-i}}}[h(X,z\_j)],y\_j)\frac{1}{N}\partial\_x h(x,z_j)\right|\right| \leq \frac{R'}{\lambda}.
$$
And the second term in the exponent is $\frac{2\lambda’}{\lambda}$-strongly convex. Therefore, we get LSI constant $\frac{2\lambda’}{\lambda}\exp\left( -\frac{R'^{2}}{\lambda^2} \frac{\lambda}{2\lambda'} - \frac{4R'}{\lambda }\sqrt{\frac{\lambda}{2\lambda'}}\right)
= \frac{2\lambda’}{\lambda}\exp\left( -\frac{R'^{2}}{2\lambda \lambda'} - \frac{4R'}{\sqrt{2\lambda\lambda'}}\right)$.
While this result is briefly stated in Example 3.5, we will include the above derivation in the revised version to enhance accessibility and transparency.
[1] S. Chewi et al., Uniform-in-n log Sobolev inequality for the mean-field Langevin dynamics with convex energy. 2024.
**Experiment and comparisons with prior PoC error bounds**
Compared to prior results [1], which yield a uniform-in-$N$ LSI constant: $\exp\left( - \frac{1}{\lambda’} - \frac{1}{\lambda\lambda’} - \frac{1}{\lambda^2\lambda’^3}\right)$, our bound demonstrates significantly improved dependence on $\lambda, \lambda’ \to 0$, leading to faster convergence in time.
Furthermore, a major improvement over [2,3] is that our particle approximation error bound is independent of $\lambda$. In contrast, earlier works suggested an exponential dependence on $\lambda$, which was overly pessimistic. To support this, we empirically investigate the effect of $\lambda$ under varying $N$ in Appendix B.2, and we did not observe such exponential blow-up, further reinforcing the practical relevance of our theoretical improvement. This highlights the importance of our contribution in tightening the gap between theoretical bounds and empirical observations. Although exactly verifying uniform bounds through experiments remains challenging, improving these theoretical bounds is an important fundamental research topic.
[2] F. Chen et al., S. Uniform-in-time propagation of chaos for mean field langevin dynamics. 2022.
[3] Suzuki, T., Wu, D., and Nitanda, A. Convergence of mean-field Langevin dynamics: time-space discretization, stochastic gradient, and variance reduction. NeurIPS, 2023. | Summary: The paper establishes improved uniform-in-time propagation of chaos bounds for MFLD by removing the exponential dependence on entropy regularization, and applies this result to propose a model ensemble strategy.
Claims And Evidence: The central claim of the paper is that it establishes an improved PoC result for MFLD by eliminating the exponential dependence on the $\lambda$ in the particle approximation error. This claim is clearly stated and mathematically proved in Theorem 3.7.
The derivation is supported by technical assumptions (Assumptions 3.2–3.4) and intermediate results such as Lemma 3.6. However, these assumptions are relatively strong and not well justified in practice. For example, the directional log-Sobolev inequality and the boundedness/Lipschitz conditions on model components may not hold in typical neural network architectures (e.g., ReLU activations or unbounded weights). Example 3.5 attempts to justify the assumptions but does not explicitly verify that Assumptions 3.2–3.4 are satisfied. Instead, it introduces additional constraints that further limit practical applicability.
The paper also claims a practical contribution via a model ensemble strategy derived from the theoretical insights. However, the empirical validation is limited:
- The experiments do not show how the approximation error scales with $N$ or $\lambda$, nor do they examine behavior in the small-$\lambda$ regime where prior results are known to break down.
- The ensemble setup uses $M$ independent networks of size $N$, which increases the total parameter budget and may lead to an unfair comparison under a fixed compute or model size constraint.
Methods And Evaluation Criteria: The theoretical methods used in the paper seem sound. Although I am not an expert in optimal transport and did not check the proofs in the appendices in full detail, the use of Wasserstein gradient flows and functional inequalities seems fine and consistent with prior literature.
However, the evaluation criteria in the experimental section are limited and not well aligned with the core theoretical contributions. The paper does not empirically evaluate key aspects such as:
- Whether the theoretical results still hold when Assumptions 2.1 and 3.2–3.4 are violated in practice.
- How the particle approximation error scales with $N$ (number of neurons/particles),
- How performance is affected by varying the entropy regularization parameter $\lambda$,
- Whether the improved $O(1/N)$ convergence rate in Theorem 3.7 matches empirical trends,
Moreover, the ensemble strategy is only evaluated in the context of LoRA fine-tuning and lacks benchmarks on standard deep learning tasks (e.g., training deep neural networks from scratch on CIFAR-10 or ImageNet). The choice of merging $M$ independent networks of size $N$ each is not compared to more realistic alternatives under a fixed budget constraint (e.g., $M$ networks of size $N/M$), which weakens the practical relevance of the proposed approach.
Theoretical Claims: No
Experimental Designs Or Analyses: Please check in the section of Methods And Evaluation Criteria.
Supplementary Material: I review the appendices B and C.
Relation To Broader Scientific Literature: This work removes that dependence by introducing a directional log-Sobolev inequality, but the lack of comprehensive experimental study weaken the connections to broader machine learning practice.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: NA.
Other Comments Or Suggestions: NA.
Questions For Authors: 1. What is the role of the regularization term $r(x)$ and the entropy regularization term in the theoretical analysis? Do the MFLD framework and the improved PoC result still hold in the absence of $L^2$ or entropy regularization?
2. Could you provide more intuition behind Assumptions 3.2 and 3.4? Specifically, how do these assumptions contribute to the analysis, and in what types of neural network architectures or setups might they realistically hold?
3. The assumption $\sup_{x,z} |h(x,z)| \le R$ seems nontrivial. In which practical scenarios or network parameterizations does this condition hold? Can you provide concrete examples?
4. The ensemble strategy seems unclear in terms of fair comparison. You consider $M$ independent networks each with $N$ neurons, but under a fixed computational or model-size budget, this setup may be suboptimal. A more realistic comparison might involve $\sqrt{N}$ networks each with $\sqrt{N}$ neurons, totaling $N$ neurons overall. In that setting, the bound in Theorem 4.4 appears similar or potentially worse due to the additional error term. Could you clarify why the proposed ensemble strategy is justified and whether it offers a real advantage under fixed resource constraints?
5. Does your theoretical framework for MFLD imply global convergence to the minimizers of the loss functionals $F_0(\mu)$ and $F_0^{(N)}(\mu^{(N)})$, similar to what is established in NTK theory? In the NTK setting, global convergence can be shown without requiring regularization. By contrast, your analysis incorporates both entropy and $L^2$ regularization. While $F_0(\mu)$ is convex over the space of distributions, it is unclear whether this alone is sufficient to guarantee global convergence of the dynamics. Could you clarify what kind of convergence your results guarantee (e.g., global vs. local), and whether additional assumptions are necessary to establish global convergence in your setting?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for reading our paper.
__Assumption 2.1, 3.2–3.4, Example 3.5, and Q3__
Assumptions 2.1, 3.2–3.4 are all satisfied in several settings considered in the mean-field Langevin literature (e.g., [1–6]). Basically, these assumptions follow for two-layer NNs with smooth and bounded activation functions. For example, under the typical loss functions (e.g., logistic and squared losses) and L2 regularization, the two-layer neural networks with the following activation function $h(x,z)$ satisfy the assumptions [4,5]: (1) $\sigma_2(r \sigma_1(w^\top z + b ))$, (2) $\sigma_2(r) \sigma_1(w^\top z +b)$, (3) $\sigma_1(w^\top z +b)$, and (4) $\sigma_1(w_1^\top z + b_1 ) + \sigma(b_2))$, where $\sigma_i$ are bounded activation functions such as tanh and sigmoid, $x=(w_1,b_1,r)$ is the parameter of each neuron, and $z$ is an input data. The last form is also discussed in Section 4.2 of our paper. While our theory does not cover ReLU activations due to their unboundedness and non-smoothness, we note that such assumptions (bounded, smooth activations) are standard in the mean-field and Langevin literature (see [3], Limitation section).
The above models also satisfy the constraints introduced in Example 3.5, and thus meet Assumptions 2.1 and 3.2–3.4. Specifically, in Example we impose: (a) $\sup_{x,z}|h(x,z)|\leq R$, (b) $\ell(a,y)$ is convex and L-Lipschitz smooth w.r.t. $a\in \mathbb{R}$, and (c) $\sup_{|a|\leq R, y \in \mathcal{Y}, x \in \mathbb{R}^d, z\in \mathcal{Z}} \|\partial_1 \ell(a,y)\partial_x h(x,z)\| \leq R’$. Typical losses such as logistic and squared loss satisfy (b). Given that $\sigma_i$ are bounded and $\ell$ is L-smooth (i.e, boundedness of partial derivative w.r.t. $a$), conditions (a) and (c) are also satisfied.
We will incorporate these concrete examples to improve accessibility and clarity.
[1] S. Mei et al., *PNAS*, 2018
[2] A. Nitanda et al., *AISTATS*, 2022
[3] L. Chizat, *TMLR*, 2022
[4] F. Chen et al., 2022
[5] T. Suzuki et al., *NeurIPS*, 2023
[6] A. Nitanda, *NeurIPS*, 2024
__Q1/Q2__
Assumption 3.4 quantifies the nonlinearity of $F_0$ with respect to the distribution. If $F_0$ is linear, MFLD reduces to a standard Langevin dynamics over $N$ independent particles. In this case, the joint distribution $\mu_t^{(N)}$ is the product measure $\mu_t^{\otimes N}$ of each particle, implying $KL(\mu_\infty^{(N)}\|\mu_*^{\otimes N})=0$ at the optimal joint distribution $\mu_\infty^{(N)}=\mu_*^{(N)}$ attained at $t=\infty$. However, in general case of nonlinear functional, there should be additional error as evaluated in Lemma 3.6; $\frac{\lambda}{N}KL(\mu_\infty^{(N)}\|\mu_*^{\otimes N})\leq \frac{B}{N}$ at the optimal solution.
Thus, the strength of nonlinearity $B$ controls the deviation from independence among particles.
Assumption 3.2 requires that the conditional distributions $\nu_{i|-i}$ satisfy an LSI, ensuring concentration of distribution of each particle. This assumption is also satisfied under the setting in Example 3.5 (for the derivation see Lemma 6 in [7]). Here, the regularization $r(x)$ is essential to encourage such concentration, and the entropy term corresponds to the Gaussian perturbation in the method.
[7] S. Chewi et al., 2024
__Experiments (scalability w.r.t. $M,N,\lambda$) and Q4__
Scalability with respect to $M$ and $N$ is empirically validated on two-layer NN with synthetic datasets (see Fig 1). The effect of $\lambda$ is examined in Appendix Sections B.2 and B.3.
Our merged method suggests a nontrivial choice of $M$ and $N$. Given a fixed computational budget $K = MN$, Theorem 4.4 yields the bound: $\frac{1}{K}+\frac{1}{\sqrt{MK}}+\frac{M}{K}$ at the solution, ignoring irrelevant constants for simplicity. This bound is decreasing on $M \in [1, (K/4)^{1/3}]$ and hence the optimal choice is $M \sim (K/4)^{1/3}$ that achieves the minimum approximation error $\frac{1}{K} + \frac{C}{K^{2/3}}$ for some constant $C$.
__Global convergence and Q1/Q5__
Our MFLD theory establishes global convergence of noisy gradient descent to the global minimizer of the un-regularized objective. Specifically, when $r(x) = \lambda' ||x||^2$, the regularization (i.e., $\mathbb{E}[r] + \lambda \mathrm{Ent}$) coincides with the KL divergence from a Gaussian distribution. Hence, minimizing $\mathcal{L}(\mu)$ leads to convergence toward minimizing $F_0$, up to a $\lambda$-dependent error shrinking to $0$ as $\lambda \to 0$.
Importantly, optimization in the mean-field regime is more challenging than in the NTK regime, as it involves solving a truly non-convex problem. In contrast, NTK theory effectively linearizes the model and neurons evolve near initialization. Actually, the mean-field regime is known to exhibit *feature learning* behavior [8,9], deviating from NTK-regime.
[8] L. Chizat et al. On Lazy Training in Differentiable Programming. *NeurIPS*, 2019
[9] G. Yang and E.J. Hu. Tensor Programs IV: Feature Learning in Infinite-Width Neural Networks. *ICML*, 2021
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. I appreciate the clarifications.
That said, I still have some concerns—particularly regarding the bounded activation assumption, which I don’t think is trivial. In modern practice, unbounded activations like ReLU and GELU are widely used due to their optimization benefits, while bounded activations (e.g., tanh, sigmoid) can slow down training and limit expressivity. Moreover, from a statistical viewpoint, the distinction is substantial: if x is sub-Gaussian, then $\sigma(x)^$2 becomes sub-exponential when $\sigma$ is unbounded, but remains sub-Gaussian if $\sigma$ is bounded. This significantly affects tail behavior and concentration properties.
Additionally, the experiments still don’t address key concerns:
- Robustness when the assumptions (e.g., boundedness) are violated;
- Scaling behavior with $n$ and $\lambda$ in realistic setups;
- Fair comparisons for the ensemble method under fixed compute or model size constraints.
Given these factors, I decided to maintain my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for the additional comments.
First, we note that convergence results with statistical guarantees under bounded activation functions have been studied in the literature, and our work provides certain improvements in this line of research.
**Global convergence under bounded activation functions.** We would like to clarify that convergence in our setting does not necessarily imply achieving zero training error, but rather convergence to the global minimum $F(\mu_*)$ of the objective. While boundedness constraints may limit the ability to perfectly fit the training data especially when the boundedness is tight, they do not inherently make the optimization problem more difficult.
To illustrate this, consider the setting where each neuron takes the form $R h(x, z)$, as used in [10], with the $L_2$ regularizer $r(x) = \lambda' ||x||^2$, where $R$ is a hyperparameter controlling boundedness and $h$ is a bounded function. As an extreme case, suppose $R\sim 0$. Then, $F_0$ becomes nearly a quadratic function which is very easy to solve. Generally, this illustrates how L2-regularization leads to a concentration of low-loss regions, facilitating the search for the global optimum. This view is closely aligned with the perspective in the sampling theory.
Actually, our theory does not currently cover ReLU, but we emphasize that boundedness does not inherently make optimization harder as seen above.
**Statistical performance.** We fully agree that boundedness plays a critical role in controlling statistical performance. In fact the paper [10] explicitly incorporates this by carefully selecting the hyperparameter $R$ to achieve strong generalization guarantees. Our convergence result can be also applied to such settings and, as discussed in our paper, offers certain theoretical improvements over prior work.
**Experiments.** Since our submission is primarily theoretical, we believe additional experiments under settings that violate our assumptions (e.g., unbounded activations) are beyond the scope of the current work. That said, we have included experiments under realistic conditions with LoRA where our method shows significant improvements in accuracy under fixed compute budgets. For more details, please see our response to Reviewer i5RL.
[10] T. Suzuki et al. Feature learning via mean-field langevin dynamics: classifying sparse parities and beyond. NeurIPS, 2023. | null | null | null | null | null | null |
Synthesizing Images on Perceptual Boundaries of ANNs for Uncovering and Manipulating Human Perceptual Variability | Accept (poster) | Summary: This paper studies individual perceptual variability by generating controversial stimuli—images perceived differently by various individuals. To do so the authors 1) sample images on the perceptual boundary of ANNs, 2) collect subject-specific labels through psychophysics experiments on the previously generated images, 3) train individually aligned neural network classifiers and 4) generate images eliciting divergent responses between individuals. The authors demonstrate the validity of their method with human experiments.
Claims And Evidence: The authors claim their computational framework can effectively produce controversial stimuli that uncover human perceptual variability. Evidence includes i) human experimental validation, demonstrating that synthesized images indeed elicit varying perceptual judgments and ii) various quantitive analyses (entropy and accuracy analysis).
Methods And Evaluation Criteria: The methods combine i) perceptual boundary sampling from ANNs, 2) individually aligned and 3) generation of images that elicit divergent responses between individuals. While the article is very clear and well written in general, I found section 3, describing the perceptual sampling method, not clear enough. It would have been useful to detail more how the uncertainty and controversial guidance integrate into the decision process.
The evaluation process relies on human experiments, which makes sense for this article. In general, I found the method clear (except section 3), and the evaluation criteria are relevant.
Theoretical Claims: This is not a theoretical claim, but the authors assert that their diffusion-based method produces more "natural" controversial stimuli compared to existing approaches. This claim, however, is insufficiently supported, especially given the comparison is largely limited to MNIST rather than photorealistic domains.
Experimental Designs Or Analyses: Experiments predominantly focus on MNIST. The effectiveness of the method on ImageNet is briefly demonstrated but not thoroughly analyzed. Detailed analyses demonstrating perceptual boundary manipulations on complex datasets would substantially strengthen the experimental claims.
Supplementary Material: Essential information regarding diffusion model architecture, classifier details, and fine-tuning procedures are insufficiently detailed in the supplementary materials. Important points, such as classifier architecture, pre-training datasets, and exact fine-tuning targets, are either missing or unclear.
Relation To Broader Scientific Literature: The paper aligns well with existing literature, addressing perceptual variability and generative modeling approaches.
Essential References Not Discussed: I have not noticed any important references that were not discussed
Other Strengths And Weaknesses: Strengths:
* Well motivated and clearly written.
* Successfully demonstrates the possibility of manipulating perceptual variability.
Weaknesses:
* Insufficient clarity and detail regarding the diffusion guidance mechanism.
* Limited analysis beyond MNIST dataset.
* Lack of clarity regarding classifier architecture and fine-tuning specifics
Other Comments Or Suggestions: * Clearly label axes in Figure 3a to improve readability and comprehension (e.g., akin to Figure 1 from the Golan et al. article).
* Correct the referencing error: Figure A.2 should be in the supplementary material, not the main article.
Questions For Authors: * How exactly are the uncertainty or controversial guidance signals integrated into the diffusion process?
* Are you using classifier-free guidance diffusion models, and if so, how are the dual-label conditions handled?
* Which classifiers (architectures and specifics) were tested for generating controversial stimuli?
* Could you clarify precisely how fine-tuning is conducted (GroupNet, IndivNet, BaseNet), and what are the exact targets for population-level fine-tuning?
* What prevents applying the full analysis presented for MNIST to more complex datasets like ImageNet?
* Can you discuss how the generative model’s biases impact the validity of perceptual variability experiments (versus GAN-based or other type of generative models)?
Ethical Review Flag: Flag this paper for an ethics review.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Response to reviewer Aam6
We sincerely thank the reviewer for the support of our work. Below we address the reviewer’s concerns and questions:
1. **Question:**
How exactly are the uncertainty or controversial guidance signals integrated into the diffusion process?
**Response:**
The uncertainty and controversial guidance signals are integrated into the diffusion process using a classifier guidance method. More details can be found in Appendix A.2.
2. **Question:**
Are you using classifier-free guidance diffusion models, and if so, how are the dual-label conditions handled?
**Response:**
We adopted classifier guidance methods for all of our experiments. Although classifier-free guidance diffusion models may offer interesting insights, they were not used in our work. In our approach, all guidance is introduced by the classifiers, and the dual-label conditions are handled by our proposed controversial guidance and uncertainty guidance.
3. **Question:**
Which classifiers (architectures and specifics) were tested for generating controversial stimuli?
**Response:**
For generating controversial stimuli using the base models (trained from scratch on the MNIST dataset), all five models are paired with each other. The guidance outcome results are presented in Figure A.14.
4. **Question:**
Could you clarify precisely how fine-tuning is conducted (GroupNet, IndivNet, BaseNet), and what are the exact targets for population-level fine-tuning?
**Response:**
We apologize for any confusion. For detailed information on the fine-tuning process, please refer to point 6 of our rebuttal to Reviewer 62LP. The goal of the population-level fine-tuning is to align the models with the population-level characteristics. Starting from GroupNet for the fine-tuning of IndivNet provides the model with a human group-level prior and helps prevent overfitting, particularly since the varMNIST-i dataset contains only a small amount of data.
5. **Question:**
What prevents applying the full analysis presented for MNIST to more complex datasets like ImageNet?
**Response:**
Please refer to point 1 of our rebuttal to Reviewer YcpF.
6. **Question:**
Can you discuss how the generative model’s biases impact the validity of perceptual variability experiments (versus GAN-based or other types of generative models)?
**Response:** We chose classifier-guided diffusion models for their superior performance, stability, and flexibility. While we explored alternatives (e.g., VAEs and prior-free guidance[1], as shown in Figure A.3), none achieved the quality or precise individual alignment that our approach provides.
We acknowledge that though a comprehensive comparison of generative model biases would indeed provide more insights, it would require developing new methodologies based on various backbone models, which falls outside the scope of this work.
7. **Question:**
The authors assert that their diffusion-based method produces more "natural" controversial stimuli compared to existing approaches. This claim, however, is insufficiently supported, especially given the comparison is largely limited to MNIST rather than photorealistic domains.
**Response:**
We apologize for any confusion in our writing. By "natural," we mean stimuli that are closer to the original distribution of the dataset. For example, in Figure A.3, stimuli generated by methods without a prior would not be recognized as digits by human participants, thereby classifying them as out-of-distribution or "unnatural" in our terms. We deliberately chose this terminology to distinguish our approach from others, such as the one proposed by Golan [1]. Although Golan’s method can generate an image x that causes classifier f1 to label it as y1 and classifier f2 as y2, it fails to produce images that human participants recognize as digits—a shortcoming that our method effectively overcomes.
**References:**
1. T. Golan, P. C. Raju, and N. Kriegeskorte, "Controversial stimuli: Pitting neural networks against each other as models of human cognition," *Proceedings of the National Academy of Sciences*, vol. 117, no. 47, pp. 29330–29337, 2020. | Summary: The functional alignment between artificial neural networks (ANNs) and the human visual system has been a major hot topic in recent years. In this study, the authors generated images that lie on the perceptual boundaries of various ANNs and examined their relationship with individual differences in human perception. Experimental results using MNIST demonstrated that the images generated by this method effectively explain individual variability in human category judgments and can be used to manipulate perceptual variability.
Claims And Evidence: The study comprehensively presents its claims and supporting experiments. However, the organization of the paper is not well-structured.
In general, it is difficult to derive generalizable conclusions only from the MNIST dataset due to low diversity, and analysis using natural images is necessary. The Introduction and Methods sections describe the paper as if this study only used MNIST. However, in Figure 4b, natural image data is introduced without any prior explanation, and the figure result of perceptual variability suggests that natural images are more appropriate for the analysis. It is only in Section 5.2 that the use of natural images is explicitly mentioned, but the results are only in the Appendix.
Instead, the authors should restructure the paper and frame while including the results obtained from natural images, which are more relevant for discussing perceptual variability.
Methods And Evaluation Criteria: The MNIST dataset is not suitable for examining human perceptual variability, as evident from Figure 4b, where participants' judgments appear to be highly consistent. This suggests that MNIST lacks the complexity necessary to capture meaningful individual differences in perception.
Theoretical Claims: N/A. Theoretical (mathematical) proof was not conducted in this manuscript.
Experimental Designs Or Analyses: In addition to reporting the results, the authors should provide further analysis to explain why fine-tuning performance varies across different model architectures. A deeper investigation into the underlying factors driving these differences would strengthen the study's findings.
Supplementary Material: As mentioned above, the results from natural images should be incorporated into the main text rather than being placed in the supplementary material. These findings should be presented as the core focus of the paper.
Relation To Broader Scientific Literature: This study may provide broader insights into understanding personalized models, which take into account individual differences across populations, including individuals with mental disorders or neurodevelopmental conditions. Such models are needed for appropriate diagnosis of these individuals.
Essential References Not Discussed: Appropriate references are discussed in this manuscript.
Other Strengths And Weaknesses: Other weakness:
The use of technical terms in the paper lacks consistency and deviates from standard terminology in cognitive science. For example, a numerical category classification task is not typically referred to as "decision making."
Additionally, the paper alternates between terms like "decision boundaries of classifiers" and "ANN perception boundary," suggesting that the authors may conflate perception and decision-making processes. The terminology should be clarified and used consistently to avoid confusion.
Other Comments Or Suggestions: In Figure 4, the colors in the legend do not match those in the bar graph. The authors should ensure consistency between the legend and the figure for clarity.
Questions For Authors: Are there specific reasons showing the large error bars in the customized dataset for guidance success rates in Figure 6c?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Response to reviewer YcpF
We sincerely thank the reviewer for the support of our work. Below we address the reviewer’s concerns and questions:
1. **Comment:**
The MNIST dataset is not suitable for examining human perceptual variability, as evident from Figure 4b, where participants' judgments appear to be highly consistent. This suggests that MNIST lacks the complexity necessary to capture meaningful individual differences in perception.
**Response:**
We agree with the reviewer that in the MNIST dataset participants' judgments appear to be highly consistent and are less complex than natural images. We conduct the major experiments using handwritten digits for two main reasons:
- **Efficiency:** The models are much easier to train and require less time, which is very important for a large-scale behavioral experiment like ours.
- **Perceptual Variability:** As mentioned by Reviewer 62LP and Reviewer YcpF, perceptual variability is harder to evoke on handwritten digits. If we can evoke perceptual variability even on a highly consistent dataset such as MNIST, then it could be applied to more complex datasets where human perceptual variability is more diverse. Based on this assumption, we evaluated our framework on natural images and observed that perceptual variability is indeed larger on natural images than on handwritten digits. Although further experiments on natural images were not conducted, it is reasonable to assume that individual perceptual boundaries are more complex on natural image datasets. This complexity might require additional rounds of experiments or a parameter-efficient method for finetuning(e.g., LoRA) as the models would become bigger and more complex. We plan to conduct more experiments and analysis on natural images in future work.
We hope the reviewer can agree with our considerations.
2. **Comment:**
In addition to reporting the results, the authors should provide further analysis to explain why fine-tuning performance varies across different model architectures. A deeper investigation into the underlying factors driving these differences would strengthen the study's findings.
**Response:**
We appreciate the reviewer's suggestion, as further analysis of the differences in fine-tuning performance across various model architectures could indeed provide valuable insights. However, the primary focus of this paper is to demonstrate the feasibility of aligning humans and AI using our method and to explore the potential for manipulating perceptual variability within our framework. Given the limited space available, we believe that an in-depth analysis of architectural differences would be better suited for a separate, more focused study.
3. **Comment:**
The use of technical terms in the paper lacks consistency and deviates from standard terminology in cognitive science. For example, a numerical category classification task is not typically referred to as "decision making." Additionally, the paper alternates between terms like "decision boundaries of classifiers" and "ANN perception boundary," suggesting that the authors may conflate perception and decision-making processes. The terminology should be clarified and used consistently to avoid confusion.
**Response:**
Thank you for pointing out this inconsistency. We will pay more attention to the use of terms and revise the text to ensure consistency with standard cognitive science terminology.
4. **Comment:**
In Figure 4, the colors in the legend do not match those in the bar graph. The authors should ensure consistency between the legend and the figure for clarity.
**Response:**
We thank the reviewer for highlighting this issue. We will revise the figure to ensure that the legend colors match those used in the bar graph.
5. **Question:**
Are there specific reasons showing the large error bars in the customized dataset for guidance success rates in Figure 6c?
**Response:**
We admit that the customized manipulation experiment can be difficult to conduct, and the effect of manipulation is largely influenced by the individual status of the participants due to the need for precise alignment with each participant. Under these circumstances, large error bars can occur. Despite the large error bars and relatively low improvement, our statistical analysis confirmed that the results are statistically significant (p < 0.001). | Summary: This paper studies the human perceptual judgements by generating controversial stimuli that lie close to the boundary between different classes. The experiments first show that finetuning vision networks on data collected from human judgements enables these models to better capture the human behavior. They then show that using these models they can generate new stimuli that can sometimes specifically bias individuals towards particular choices.
## update after rebuttal
Several issues were clarified. The discussion helped with understanding the practical issues in scaling the approach to natural images. I increased my score by 1 as a result. The authors agreed to make changes to address the issues and unclarities.
Claims And Evidence: - The success rate in selective manipulation of human behavior is relatively low, showing limited success in using the proposed approach. This is especially true for handwritten digits with ~20% success rate. Surprisingly, while the initial experiment using natural images seem to be much more successful, none of the following experiments were conducted using natural stimuli.
- section 5.2: the IndivNet only improves the behavioral prediction accuracy by 5% over groupNet, yet it is claimed that this approach captures individual differences in perceptual judgments. The result seem to suggest that the model training mostly captures the group effect in this behavior.
Methods And Evaluation Criteria: The methods are appropriate.
Theoretical Claims: No new theory was proposed.
Experimental Designs Or Analyses: They are generally appropriately designed although I have several questions about the details of how they are conducted.
Supplementary Material: No supplementary material was provided
Relation To Broader Scientific Literature: The introduction and discussion sections puts the paper into the perspective of the prior literature. Specially the work by Golan and Kriegeskorte is very closely related to the current work.
Essential References Not Discussed: All relevant work were cited
Other Strengths And Weaknesses: Strengths:
- the idea of capturing individual differences in human subjects by collecting personal data and training neural networks on them is interesting.
- the paper was well structured, mostly well-written with clear figures
Weaknesses:
- the dataset is almost too easy and restrictive
- despite being well written many details were missing
- overall, the method does appear to be very effective, especially in the context of capturing individual differences and successfully biasing judgements in a selective way
Other Comments Or Suggestions: typos: line 161 additional parentheses
line 173: incorrect figure reference
fig A11 caption: incorrect subplot indicators
Questions For Authors: - Were subjects given extended time or was there a time limit in labeling the images? This is important because, some of the individual differences may be due to arbitrary position of gaze that may have influenced the declared labels.
- line232: varMINST-i dataset is not defined. Is that a subset of samples labeled by one individual? If so, was one model trained per individual? The dataset and procedure should be better explained
-line 236: the description of model training is confusing. The first part of the description suggests that the network was jointly trained on two datasets but the latter part and the term "finetuning" suggests first training on mnist then on vamnist.
- were there shared images across different individuals? how were the labels for repeated images from different individuals combined?
- It is unclear whether the networks used in the study VGG, VIT, CORnet were trained from scratch or a pretrained network was used. The text gives me the impression that they were trained from scratch but the number of parameters in these networks and the relatively small dataset size makes me doubt that.
- there are no references to the models used in the study
- figure 6: it's unclear what the "individually customized dataset" is. Not explained.
Ethical Review Flag: Flag this paper for an ethics review.
Ethics Expertise Needed: ['Responsible Research Practice (e.g., IRB, documentation, research ethics, participant consent)']
Ethical Review Concerns: Human behavior experiments require IRB or similar approvals but they were not mentioned in the text.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Response to reviewer 62LP
We sincerely thank the reviewer for the positive feedback. Below we address the reviewer’s concerns and questions:
1. **Comment:** The success rate in selective manipulation of human behavior is relatively low, showing limited success in using the proposed approach. This is especially true for handwritten digits with ~20% success rate. Surprisingly, while the initial experiment using natural images seem to be much more successful, none of the following experiments were conducted using natural stimuli.
**Response:** Please refer to point 1 of the rebuttal to Reviewer YcpF.
2. **Comment:** Section 5.2: The IndivNet only improves the behavioral prediction accuracy by 5% over GroupNet, yet it is claimed that this approach captures individual differences in perceptual judgments. The result seems to suggest that the model training mostly captures the group effect in this behavior.
**Response:** We believe the relatively small improvement is due to the similarity between the individual perceptual boundary and the group-level perceptual boundary. We hope the reviewer agree with us that it is reasonable to assume that individuals, in general, are close to the group, resulting in a relatively small improvement.
3. **Response to typos:**
We thank the reviewer for pointing out these mistakes. We will reorganize the appendix and revise the text in a future version.
4. **Question:** Were subjects given extended time or was there a time limit in labeling the images?
**Response:** In the major experiments, all subjects were given extended time to reduce random effects that could impact the experiment, such as arbitrary gaze positions or unexpected distractions.
5. **Question:** (Line 232) The varMNIST-i dataset is not defined. Is that a subset of samples labeled by one individual? If so, was one model trained per individual? The dataset and procedure should be better explained.
**Response:** The varMNIST dataset consists of images with multiple labels (labeled by different participants or trials, as described in the paper). Each participant performed around 500 trials on different images. The dataset corresponding to each participant is referred to as varMNIST-i, and one model is trained per individual. We appreciate your valuable suggestions and will clarify the dataset and procedure in future revisions to the main text.
6. **Comment:** (Line 236) The description of model training is confusing. The first part suggests that the network was jointly trained on two datasets, but the latter part and the term "finetuning" suggest first training on MNIST and then on varMNIST.
**Response:** The training process is conducted as follows:
- **Base Model:** First, we train a model using only the MNIST dataset.
- **Group Model:** Next, we finetune the base model to align it with the human group level. The finetuning dataset is constructed by mixing MNIST data into our varMNIST data, a common technique to prevent overfitting and model forgetting. This process yields the group model.
- **Individual Model:** Finally, based on the group model, we perform another finetuning at the individual level to align the model with each individual. This finetuning dataset is created by mixing MNIST, varMNIST, and varMNIST-i together. The training and evaluation sets are carefully divided so that even if there is an overlap between varMNIST and varMNIST-i, nothing in the evaluation set appears in the training set. Parameter details can be found in Appendix C.2.
7. **Question:** Were there shared images across different individuals? How were the labels for repeated images from different individuals combined?
**Response:** Yes, there are shared images across different individuals. Each image-label pair is treated as a trial and used in the finetuning process.
8. **Question:** It is unclear whether the networks used in the study (VGG, ViT, CORnet) were trained from scratch or if a pretrained network was used.
**Response:** The base models are trained from scratch. The group models are finetuned from the base models, and the individual models are finetuned from the group models, as explained in point 6.
9. **Comment:** There are no references to the models used in the study.
**Response:** We sincerely appreciate your suggestion and will add references for these models in future revisions.
10. **Comment:** Figure 6: It is unclear what the "individually customized dataset" is.
**Response:** The individually customized dataset is generated under the guidance of finetuned individual models to better evoke variability and bias participants toward certain directions.
11. **Ethics**
**Response:** We mentioned the ethics approval in Appendix B.2.2. Regarding human data collection, we can provide ethics documents and participant agreements upon request. We will incorporate these details into the main text in future revisions.
---
Rebuttal Comment 1.1:
Comment: Thank you for the additional clarifications.
1. Re comment1: finetuning CNN models should be feasible even in academic settings. As I mentioned in my original comment, the initial experiments are more successful with the natural images, and I expected to see at least some further results on that aspect. I'm unsure whether the "efficiency" argument is justified here. Can you show any indication that you could generalize the approach to that setting?
2. Re comment2: I agree that subjects would mostly agree in their behavioral judgements. Can you quantify how much of the remaining accuracy gap is due to group-effect vs. individual?
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for the thoughtful and constructive feedback.
### Response 1
a. We first conducted collection and manipulation experiments on the digit dataset, followed by collection experiments on natural images. Due to time constraints and high experimental costs, we were unable to complete the manipulation experiments on natural images. Although natural images showed a significantly higher success rate ( ~60%, Fig. 4) compared to digits ( ~20%) in the collection experiments, fine-tuning revealed that the accuracy gap between IndivNet and GroupNet for natural images was only ~2% (Fig. a.24, compared to ~5% for digits). This suggests that the 400 samples per participant may be insufficient for adequately fine-tuning natural image classification models, and further increasing the number of trials presents practical challenges. Since the manipulation experiment relies on IndivNet accurately capturing individual preferences, we did not proceed with natural image manipulation. Our earlier mention of "efficiency" referred to this issue, though the explanation was not sufficiently clear.
b. As previously noted, while we lack follow-up experimental data, it is reasonable to assume that training IndivNet on natural images would pose greater challenges. This might require specially designed parameter-efficient fine-tuning methods (e.g., LoRA) and additional large-scale behavioral data collection. Addressing this may necessitate a dedicated follow-up study, and we hope the reviewer understands our considerations.
c. The collection experiment results (Fig. 4) show that eliciting perceptual variability is more challenging on the digit dataset, which in turn demonstrates the effectiveness of our perceptual boundary sampling method across different datasets. We also generated some stimuli based on the finetuned individual models on ImageNet, in https://anonymous.4open.science/r/Figures-7CFB/ImageNet_Individual.png. Though we did not conduct further experiments, some of the images do display potentials of manipulation applications. Thus, the success of digit manipulation experiments suggests potential applicability to natural images.
d. We appreciate the reviewer’s feedback and will add these explanations to Section 6, Discussion and the appendix to clarify why natural image manipulation experiments were not pursued.
---
### Response 2
Our dataset was specifically designed to elicit perceptual variability, resulting in many samples that GroupNet cannot reliably predict. To facilitate understanding, accuracy can be decomposed into three types of uncertainty: **group epistemic uncertainty**, **individual epistemic uncertainty**, and **aleatoric uncertainty**. Here, individual epistemic uncertainty reflects variations due to individual differences, while aleatoric uncertainty captures intra-subject variability. Additional experiments show that increasing data volume has diminishing returns on GroupNet accuracy (Table 1), whereas IndivNet accuracy continues to improve significantly (Table 2) using VGG models. The tables are at the link https://anonymous.4open.science/r/Figures-7CFB/tables.md. We also provide a figure showing relative accuracies (improvements at a reduced data volume/improvement at full data volume) v.s. data volume at https://anonymous.4open.science/r/Figures-7CFB/ImprovementVSdataamount.png. However, since repeated presentation of the same stimulus introduces trial-to-trial interference, the impact of aleatoric uncertainty is difficult to quantify. Thus, we estimate that individual epistemic uncertainty accounts for at least a **5% accuracy gap** (i.e., IndivNet minus GroupNet), though a more precise estimate remains challenging. | null | null | null | null | null | null | null | null |
Boosting Multi-Domain Fine-Tuning of Large Language Models through Evolving Interactions between Samples | Accept (poster) | Summary: The authors propose EVolving Interaction-guided Curriculum (EVIC), a training technique that aims to improve the performance of LLM multi-domain fine-tuning. EVIC iteratively finds the most “helpful” samples in the training set (those that are likely to have helpful influence on the model’s overall loss), then trains on just this helpful subset. The authors conduct experiments of fine-tuning GPT-4 to code, math and general reasoning domains, comparing EVIC to four prior works.
Claims And Evidence: Claims are supported
Methods And Evaluation Criteria: - Lines 159-160 (and other places): when examining the interactions among samples over time, do you find that the interactions eventually stabilize and evolve less? How does that time to stabilization compare with the model convergence time?
- Line 163: How asymmetric are these interactions? Is there any chance that the asymmetry is just due to random noise or do you have any other hypothesis as to why these interactions are asymmetric?
- EVIC begins with a “warm-up” phase, where 5% of samples are randomly selected to start training with. Because 5% is such a small proportion, is the method’s performance highly dependent on which samples are initially selected? Have you tried EVIC with initial portions other than 5%?
- It would be interesting to see a histogram of how often samples are chosen as helpful during training: for instance, a bar for samples never chosen, a bar for samples chosen once, twice, etc.
- If you are training on domains with datasets of varying sizes, will EVIC negatively impact the performance of the model on the rarer domain? For instance, suppose you are training a model to perform n different tasks, where n-1 of the datasets have 10000 samples and the nth dataset has 100 samples. Will the strategy of focusing only on the samples that appear most helpful overall result in neglecting the performance of the smaller dataset?
Theoretical Claims: N/A
Experimental Designs Or Analyses: - EVIC performs well in the evaluations compared to prior works (Table 2)
- There are a strong number of baselines and related works included in the evaluation and the evaluation appears to be well-designed by including tasks of varying sizes. However, the evaluation could be expanded and strengthened by including more models beyond GPT-4 and additional domains/datasets.
Supplementary Material: N/A
Relation To Broader Scientific Literature: Multi-domain training is a useful and important area of ongoing research, and EVIC appears to perform favorably compared to prior works in this area
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: One typo: line 252 “firness” instead of “fairness”
Other Comments Or Suggestions: Overall, the method is intuitive and offers good performance. However, the analysis and evaluations could be improved by including more tasks and comparing to prior works. These factors together have contributed to my score.
Questions For Authors: All questions are asked in the prior sections
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer zLAH,
Thank you for your valuable review. We respond to each comment as follows and sincerely hope that our response can properly address your concerns.
Figures and Tables can be found in **zLAH.md** in **https://anonymous.4open.science/r/ICML25-EVIC-D5E8**
# Methods And Evaluation Criteria
> M1: Do you find that the interactions eventually stabilize and evolve less? How does the time to stabilization compare with the model convergence time?
**Res:** We do not observe the stability of the interaction matrix. Taking Llama-3.1-8B and Mistral-7B-v0.3 as examples, the Frobenius norm of the interaction matrix after the warm-up phase, 1 iteration, 2 iterations, and 3 iterations is as follows.
- Llama-3.1-8B: 9e12 -> 5e12 -> 6e12 -> 4e12
- Mistral-7B-v0.3: 9e12 -> 2e12 -> 4e12 -> 2e12
> M2: How asymmetric are the interactions? Is there any chance that the asymmetry is just due to random noise? Do you have any other hypothesis as to why these interactions are asymmetric?
**Res:** Taking Llama-3.1-8B and Mistral-7B-v0.3 as examples, their interaction matrices consistently have more than **99.7%** of sample pairs $(i,j)$ satisfying $Int(i,j) \neq Int(j,i)$. We further analyze the proportion of pairs $(i,j)$ with opposite influence directions during training, i.e., those satisfying $sign(Int(i,j)) \neq sign(Int(j,i))$. The percentages after the warm-up phase, after 1 iteration, 2 iterations, and 3 iterations are as follows.
- Llama-3.1-8B: 19.3% -> 17.9% -> 16.7% -> 17.4%
- Mistral-7B-v0.3: 22.1% -> 21.5% -> 21.8% -> 21.1%
The asymmetry of the interaction matrix arises from the difference between each sample's original gradient $Grad$ and Adam gradient $Adam$. Since $Int(j,i) = \langle Adam(j), Grad(i) \rangle$, $Int(i,j) = \langle Adam(i), Grad(j)\rangle$, we naturally have $Int(j,i) \neq Int(i,j)$.
> M3: (1) Have you tried EVIC with initial portions other than 5%? (2) Is EVIC's performance highly dependent on which samples are initially selected?
**Res:** (1) Yes, please see Figure 3 in Section 4.3.
(2) The standard EVIC randomly samples 5% of the dataset for warm-up. To investigate the impact of warm-up samples, we have added additional experiments only using samples from code and general domains for warm-up, denoted as CodeWarmUp and GeneralWarmUp. The results are shown in **Tables zLAH-1 and zLAH-2** in the anonymous link. As shown, unbalanced warm-up sample distribution will reduce model performance.
> M4: It would be interesting to see a histogram of how often samples are chosen as helpful during training. For instance, a bar for samples being never chosen, a bar for samples being chosen once/twice, etc.
**Res:** We have added figures in the anonymous link following your suggestion.
> M5: Will EVIC negatively impact the performance of model on the rarer domain when training on domains with datasets of varing sizes?
**Res:** Imbalanced datasets can indeed hinder the learning of rarer domains. Fine-tuning on such imbalanced datasets is another important challenge in multi-domain finetuning [1,2,3]. To enhance the learning of rare domains, we can weight the interaction matrix computation in EVIC based on the sample size of each domain, increasing the probability of selecting samples from rare domains.
Extending EVIC to imbalanced datasets is a new direction, and we will continue to explore this in future work. If you are interested, we would be glad to discuss this topic further.
# Experimental Designs Or Analyses
> E1 There are a strong number of baselines and related works included in the evaluation and the evaluation appears to be well-designed by including tasks of varying sizes. However, the evaluation could be expanded and strengthened by including more models beyond GPT-4 and additional domains/datasets.
**Res:** Thanks for the positive feedback on our experimental design.
- **Regarding the models:** Our experiments use three of the most popular and widely-used base models---Mistral-7B-v0.3, Llama-3.1-8B, and Qwen2.5-14B.
- **Regarding the domains/tasks:** Since DMT is experience-baesd and cannot be directly applied to other domains (as the authors of DMT do not provide relevant experience), we **follow DMT's setting** using mixed dataset containing code, math, and general domains to **ensure fairness**. If you have any other domains or datasets of interest, we would be happy to hear from you through a rebuttal response. **While our computational resources are limited, we will make every effort to conduct additional experiments to follow your suggestions.**
# Other Strengths And Weaknesses
> W1 The "firness" in Line 252 should be "fairness".
**Res:** Thanks for pointing this out. We will correct this typo.
---
[1] Mixture-of-Skills: Learning to Optimize Data Usage for Fine-Tuning Large Language Models
[2] Massively Multilingual Neural Machine Translation in the Wild: Findings and Challenges
[3] Unsupervised Cross-Lingual Representation Learning at Scale | Summary: This paper leverages a way to estimate the training data samples' influence on each other by leveraging the gradients of Adam and projecting it into a lower dimensional space from Xia et al. 2024 [1] and iteratively using this computation in order to select samples to train in the multi-domain fine-tuning setting. They demonstrate that
[1] Xia, Mengzhou, et al. "Less: Selecting influential data for targeted instruction tuning." arXiv preprint arXiv:2402.04333 (2024).
### Update after rebuttal
Given the authors' additional experiments provided, I am inclined to raise my score to 4. I stand corrected in that the authors do show that their method can on average improve scores across different benchmarks. However, I recommend that these two points should be addressed for the updated camera ready/next version.
1. Random seeds should be computed across training runs, not LLM evaluation. Yes I do agree that there is variability in LLM evaluations, but to show consistency in performance improvement, the training run seeds are much more important.
2. The plot of the training iterations/samples vs performance that the authors provided is a great start, although it lacks details about which dataset it was conducted on. Because the novelty of this paper is not the derivation for computing influence of training samples but applying that to multi-domain finetuning, this kind of analysis of how the method is sample efficient compared to other methods seems very important.
Claims And Evidence: The claims are sound.
Methods And Evaluation Criteria: The proposed methods and evaluation are sensible for this problem.
Theoretical Claims: Yes.
Experimental Designs Or Analyses: Yes, the experimental setup seems sound.
Supplementary Material: Yes, the whole appendix.
Relation To Broader Scientific Literature: This relates to the language modeling community in investigating how to build models that can excel in different domains when trained altogether.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths
- The paper is clearly written. The problem and the proposed solution (iterative solution to estimate influence and select data samples) are clearly described. A caveat here is that the contribution of the paper isn't to derive the method using Adam gradients to calculate the influence function and it would be poignant to clarify the contributions of this paper vs leveraging insights from other works.
- The experiments are somewhat comprehensive across different benchmarks and models.
Weaknesses
- The results are generally positive, but often times they observe marginal improvement and sometimes no improvement (within the std dev) over other methods at all. For example, in the Qwen and Mistral experiments.
- The sample efficiency is an important point for this method, but Table 3 doesn't necessarily provide a holistic picture of how the evaluation metrics are evolving over the training across the different methods of multi-domain finetuning. It would be very helpful to have that as I mention in the questions below.
Other Comments Or Suggestions: 1. A curiosity is whether one can adopt the approach of leveraging test samples to calculate their similarity like in Cao et al. 2023; Wu et al. 2024) in this proposed method to calculate the influence between the test samples vs the training samples and then use the scores to select the training samples. This could verify whether influence computation and sample selection indeed are effective, by leveraging privileged information about the test samples.
2. How are the standard deviations in Table 2 calculated? How many runs of the experiments were done?
3. How expensive is computing the influence at each iteration of EVIC?
Questions For Authors: 1. Could you actually provide a more informative version of Table 3 where we can visualize the evaluation metrics over the training (x-axis being the % of total data seen and y-axis the evaluation benchmarks, for example)? It would be important to see the training dynamics and the sample efficiency that way.
2. The authors argue that iterative computation is necessary, but how does the frequency or sample selection size of each iteration change the dynamics of EVIC?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer JcLd,
Thank you for your valuable review. We respond to each comment as follows and sincerely hope that our response can properly address your concerns.
Figures and Tables can be found in **JcLd.md** in **https://anonymous.4open.science/r/ICML25-EVIC-D5E8**
# Other Strengths And Weaknesses
> W1: It would be poignant to clarify the contribution of this paper is not to derive the influence computation using Adam gradients.
**Res:** We will accordingly modify our presentation.
> W2: Often times they observe marginal improvement and sometimes no improvement (within the std dev). For example, in the Qwen and Mistral experiments.
**Res:** We confidently yet humbly believe **EVIC significantly outperforms existing methods** for the following reasons:
1. Our focus is on the **overall (AVG) performance improvement** in multi-domain fine-tuning. EVIC outperforms the second-best method in terms of AVG by 4.1, 0.8, and 1.0 on Mistral, Llama, and Qwen, respectively. We believe this improvement is **significant**, as **even a 0.5 gain on a multi-domain datasets with inter-sample conflicts is challenging**.
2. We respectfully speculate that you may find EVIC's improvement in some single domains marginal. However, please note that **EVIC consistently ranks first or second across all domains**, which is also a remarkable and challenging achievement.
> W3: Table 3 does not provide a holistic picture of how the evaluation metrics are evolving over training across different methods of multi-domain finetuning. Could you actually provide a more informative version of Table 3 where we can visualize the evaluation metrics over the training?
**Res:** Due to the deletion of intermediate results and checkpoints for some baselines, we need to retrain them. With limited computational resources, the experiment is still in progress. **We will complete it before the discussion deadline and provide more informative tables or figure as suggested.** We would greatly appreciate your understanding.
# Other Comments Or Suggestions
> S1: Can this method be adopted to calculate the influence between test samples and training samples, and use the scores to select training samples?
**Res:** The approach of calculating the influence between test and training samples is orthogonal to and compatible with our method. However, it faces challenges in multi-domain fine-tuning of LLMs. When test samples conflict (e.g., the evaluation is across different domains), even positively influencing training samples may still conflict with each other, hindering the performance. This brings us back to the core challenge of "how to conduct multi-domain fine-tuning."
> S2: How are the standard deviations in Table 2 calculated? How many runs of the experiments were done?
**Res:** We provide relevant information in Lines 254-264 (left column) of our initial submission but acknowledge it lacks detail. We will revise it as follows.
Specifically, all training is conducted once using the same random seed due to limited resources. For inference:
- HumanEval: We run model inference with a temperature of 0.3, using random seeds from 1 to 10. Then, we report the mean and standard deviation (std dev) of Pass@1 and Pass@10 using Numpy.
- GSM8K-test: We use greedy decoding with a temperature of 0.0 (so there is no std dev) and report accuracies.
- AlpacaEval 2.0: We run inference with a temperature of 0.7, using random seeds from 1 to 10. We use the AlpacaEval library, with GPT-4 as the judge, to compare model outputs against GPT-4 Turbo outputs, and report the mean and std dev of (length-controlled) win rate using Numpy.
> S3: How expensive is computing the influence at each iteration of EVIC?
**Res:** The cost of calculating influence (interactions) in each iteration is mainly dominated by the gradient computation for all samples, which is rougthly equivalent to performing one epoch of MTL. We humbly believe the additional computational cost of the interaction matrix is **acceptable and worthwhile**. For more details, please see our response to **C2 of Reviewer q9CU** due to the rebuttal length constraints.
# Questions For Authors
> Q1: Please see W3.
> Q2: How does the frequency or sample selection size of each iteration change the dynamics of EVIC?
**Res:** The higher the frequency and the fewer samples learned per iteration, the more accurate the gradient computation and interaction matrix estimation become, leading to better EVIC performance. However, excessively high frequency would result in numerous full-dataset gradient computations and extremely high costs. Therefore, in our initial submission, we simply set the frequency and sample selection size as follows.
- Sample selection size: All samples with a non-negative row sum in the interaction matrix are selected, with no limit on the number.
- Iteration frequency: After all samples selected in the previous iteration have been learned, the process moves on to the next iteration.
---
Rebuttal Comment 1.1:
Comment: ## Acknowledged
- Thank you for the clarifications to my questions, and I stand corrected that Table 2 shows that EVIC does on average improve upon the existing baselines for multi-domain finetuning. The std dev of the results are computed based on random seeds across evaluations, rather than training, which don't give me the certainty that these are statistically significant differences.
## Questions
> The approach of calculating the influence between test and training samples is orthogonal to and compatible with our method. However, it faces challenges in multi-domain fine-tuning of LLMs. When test samples conflict (e.g., the evaluation is across different domains), even positively influencing training samples may still conflict with each other, hindering the performance.
>
The intention of this suggestion was not to use it in practice for multi-domain finetuning, but rather to study, if given the oracle dataset that we want to transfer on, how effective the method is at choosing the "optimal" set of training datapoints. Depending on the time constraint, I understand if this experiment cannot be done.
> Specifically, all training is conducted once using the same random seed due to limited resources.
So, from what I read from the paper and the rebuttal, the average and std dev of Table 2 are calculated across random seeds for evaluation. But, usually the variance we care about is more about **random seed across different training runs**. It is a bit misleading in my opinion.
> We will complete it before the discussion deadline and provide more informative tables or figure as suggested.
Thank you for re-running these experiments and look forward to seeing the how the evaluation metrics evolve over training across different methods (b/c a significant point is that EVIC is more sample-efficient than the others while ultimately improving on the final performance).
If this result seems promising, I would be willing to raise my score to 4.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer JcLd,
Thank you again for your insightful comments, constructive suggestions, and positive feedback. We respond to your follow-up questions as follows and sincerely hope that our response has properly addressed your concerns. **If so, we would be profoundly grateful if you could kindly reconsider your score.** Please rest assured that *we hold your expert judgment in the highest regard*, and we sincerely hope that this request *does not cause any inconvenience or disturbance*.
---
> Q1: The intention of this suggestion was not to use it in practice for multi-domain finetuning, but rather to study, if given the oracle dataset that we want to transfer on, how effective the method is at choosing the "optimal" set of training datapoints. Depending on the time constraint, I understand if this experiment cannot be done.
**Res:** Thank you for your patient explanation and your kind understanding. Despite our best efforts, we are unable to complete this experiment before the deadline of the discussion phase due to limited computational resources. We will continue this experiment and include the results in the revised version of our paper.
---
> Q2: So, from what I read from the paper and the rebuttal, the average and std dev of Table 2 are calculated across random seeds for evaluation. But, usually the variance we care about is more about random seed across different training runs. It is a bit misleading in my opinion.
**Res:** Thank you for pointing this issue out. We report the standard deviation of the model inference results because the inference of LLMs often involves some randomness. However, we acknowledge that the expression in the initial submission is unclear, and we will make the corresponding modification in the revised version of our paper.
---
> Q3: Thank you for re-running these experiments and look forward to seeing the how the evaluation metrics evolve over training across different methods (b/c a significant point is that EVIC is more sample-efficient than the others while ultimately improving on the final performance). If this result seems promising, I would be willing to raise my score to 4.
**Res:** Thank you for your encouragement. We provide the results in **https://anonymous.4open.science/r/ICML25-EVIC-D5E8/JcLd-Reply-Rebuttal-Comment.md**. As can be seen, EVIC achieves higher performance with less training steps compared to other methods. | Summary: This work presents a curriculum learning method to improve the multi-domain fine-tuning of LLMs. Specifically, the idea is to model the Adam gradient interaction between examples and select the example with the best total benefit on learning other examples. This whole process starts with a warmup stage with around 5% of the data and an iterative process using the aforementioned method. In the evaluation on three different datasets, this method is shown to be better than simple multi-task learning and some other baselines in term of jointly learning all the tasks.
Claims And Evidence: This work presents the EVIC method for multi-domain fine-tuning. The experiments are quite convincing in demonstrating the performance improvement with EVIC and how it outperforms MTL and some other baselines. However, I have two main concerns about the evaluation:
1. There is no curriculum learning baseline in the comparison. I understand that curriculum learning methods are usually not specially designed for multi-domain fine-tuning. However, it is still really important to compare EVIC with some basic curriculum learning methods given how similar these methods are on a high level. This can also serve as ablations to demonstrate the effectiveness of the sample interaction modeling part.
2. The EVIC method seems to be really computationally expensive due to the need to compute the gradient for every example when computing the interaction matrix. This makes scaling this method to large datasets difficult. Additionally, this makes all the questions around sample efficiency questionable. From a practical perspective, the more important value that practitioners care about is how many times you compute the gradient on any example, and I don't see an efficiency advantage on that from EVIC.
Methods And Evaluation Criteria: The method makes sense on a high level, but I wonder why the authors compute sample interactions with "Adam" gradients. Momentum plays a huge role in Adam, and I feel it also heavily influences the calculation in Sec. 3.1. Do the authors have any thoughts or have the authors done analyses on this point? Additionally, lines 159-160 mention that the interaction evolves over the course of the training. How much of this evolution is due to the momentum term?
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: I can't find how important hyperparameter like M and the total length of each iteration is determined in the paper. These are very important hyperparameters for this method.
Supplementary Material: No major issues.
Relation To Broader Scientific Literature: Multi-domain fine-tuning is a practically important but relatively underexplored field. This paper introduces a novel algorithm on this based on prior literature of curriculum learning and sample influence modeling.
Essential References Not Discussed: No essential major references.
Other Strengths And Weaknesses: n/a
Other Comments Or Suggestions: 1. If the authors can add some qualitative examples of how the models select examples, it will make it more intuitive to understand how this method works.
2. Definitions of LC-WR and WR should be added to the paper when they are first introduced.
3. There are two repetitive references to Xia et al., 2024.
Questions For Authors: See above.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Dear Reviewer q9CU,
Thank you for your valuable review. We respond to each comment as follows and sincerely hope that our response can properly address your concerns.
Tables can be found in **q9CU.md** in **https://anonymous.4open.science/r/ICML25-EVIC-D5E8**
# Claims And Evidence
> C1: There is no curriculum learning (CL) baseline in the comparison. It is imporatant to compare EVIC with some basic CL methods.
**Res:** Apologies for the lack of clarity in our paper. The baselines in our initial submission (DMT and MoS) belong to **progressive CL** and **balanced CL** methods as categorized in [1,2]. We will refine this in the paper.
Additionally, we have added **vanilla CL** and **self-paced CL** as baselines. Thus, our experiments have covered **four CL method categories**. **Tables q9CU-1 and q9CU-2** in the anonymous link show that EVIC, DMT, and MoS significantly outperform other CL baselines, underscoring the importance of CL methods tailored for multi-domain fine-tuning.
> C2: EVIC seems to be computationally expensive due to the gradient computation for every sample when computing the interaction matrix.
**Res:** We humbly believe the additional computational cost of the interaction matrix is **acceptable and worthwhile**. Additionally, to reduce costs and improve efficiency, we provide some ideas on implementations and methodological improvements.
1. EVIC’s gradient computation and total cost are **less than twice** that of MTL, which is accpetable and worthwhile for real-world applications. In multi-domain LLM fine-tuning, **performance bottlenecks are more challenging than efficiency bottlenecks**, as extending training time often fails to overcome performance limits. Our proposed EVIC effectively improves the performance via iterative interaction estimation, thereby making a significant contribution.
2. However, the efficiency and cost concerns you mentioned are also important. For full dataset gradient computation, we parallelize computations across eight GPUs. **We would like to point out that there is a trade-off between efficiency and performance.** To reduce costs, we could use historical gradients of some samples without recomputing them, but this would result in inaccurate interaction estimates and thus decrease training performance. In our initial submission, **we prioritize performance over efficiency**, but in efficiency-critical scenarios, using historical gradients could be explored.
# Methods And Evaluation
> M1: Why computing interactions with "Adam" gradients? Does the momentum heavily influence the calculation in Sec. 3.1? How much of the evolution of interactions is due to the momentum term?
**Res:** Because the interactions are modeled as influences between samples during "training" and LLMs are usually trained with Adam optimizer, the "Adam" gradients naturally appears in the computation of interactions. In a nutshell, our interactions are **defined based on** Adam gradients the corresponding momentum.
We further add experiments to demonstrate the rationale behind computing interactions based on Adam gradients, where we compare EVIC with its variant that computes interactions using the inner product of the original gradients. Please see **Table q9CU-3** in the anonymous link for details due to rebuttal length constraints.
# Experimental Designs Or Analyses
> M2: I can't find how $M$ and the total length of each iteration is determined in this paper.
**Res:** We provide the relevant information in Lines 248-252 (right column) in our initial submission but acknowledge it lacks detail. We will revise it as follows.
Specifically, we set the number of iterations $M$ to be as large as possible while ensuring that the total training steps of EVIC do not exceed those of baselines to maintain fairness. Thus, $M=4,3,2$ for Mistral, Llama, and Qwen experiments, respectively. As for the length of each iteration, it refers to the number of training steps required to learn all selected samples in this iteration, i.e., $|D_m|/{\rm batch size}$.
# Other Comments Or Suggestions
> S1: Adding some qualitative examples of how the models select examples will make it more intuitive to understand how EVIC works.
**Res:** Thanks for your valuable suggestion. We have added some qualitative examples in Figure q9CU-1 in the anonymous link, but we are not sure if this is exactly what you want. **Could you please clarify your suggestion in more details so that we can better follow it?**
> S2: Definitions of LC-WR and WR should be added when first introduced.
**Res:** We will add the definitions based on [3]. Due to the rebuttal length constraints, we cannot provide the definitions here. We would greatly appreciate your understanding.
> S3: Two repetitive references.
**Res:** We will make modifications accordingly.
---
[1] Curriculum Learning: A Survey.
[2] A Survey on Curriculum Learning.
[3] Length-Controlled AlpacaEval: A Simple Way to Debias Automatic Evaluators.
---
Rebuttal Comment 1.1:
Comment: Thank you for the detailed responses and the new results! I have two follow-up comments.
1. Can you elaborate on "EVIC’s gradient computation and total cost are less than twice that of MTL"? It's not obvious to me. And despite everything you have said, do you agree that the sample efficiency claims in the original paper is a bit misleading?
2. For "Adding some qualitative examples of how the models select examples will make it more intuitive to understand how EVIC works.", I was mainly hoping to see some actual text examples so that I can have a more intuitive understanding about what example order does EVIC prefers. But you really don't have to include this in this rebuttal. It's not super critical and I'll be happy as long as you can include some examples in the final version.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer q9CU,
Thank you again for your careful review, insightful comments, and constructive suggestions. We respond to your follow-up comments as follows and sincerely hope that our response has properly addressed your concerns. **If so, we would be profoundly grateful if you could kindly reconsider your score.** Please rest assured that *we hold your expert judgment in the highest regard*, and we sincerely hope that this request *does not cause any inconvenience or disturbance*.
---
> C1: (1) Can you elaborate on "EVIC’s gradient computation and total cost are less than twice that of MTL"? It's not obvious to me. (2) And despite everything you have said, do you agree that the sample efficiency claims in the original paper is a bit misleading?
**Res:** Thank you for your question and constructive feedback.
1. This conclusion is empirical, and can be roughly estimated as follows. The additional gradient computation cost of EVIC is approximately equivalent to that of MTL training (as both require the gradients of all samples), and the gradient computation cost for updating model parameters in EVIC is less than that in MTL training, since EVIC uses fewer training steps. Taken together, the total cost of EVIC is therefore less than twice that of MTL ($a \approx c, b < c \Rightarrow a + b \lesssim2c$).
2. While this additional cost is acceptable and worthwhile, your insightful comment on *sample efficiency* is **greatly appreciated** and makes us realize that our original claim is unclear. What we intend to convey is that, *given the same amount of training samples, EVIC achieves higher performance in multi-domain LLM fine-tuning, whereas other methods are unable to surpass EVIC even with more training steps (as shown in Table 3)*. In retrospect, this intended meaning is more accurately described as "**higher performance gain per sample**" or "**higher performance-to-sample ratio**". We will **accordingly revise all statements** related to *sample efficiency* in the final version and provide a **clear definition** when the term is first introduced.
Thank you again for your thoughtful comments and suggestions.
> C2: For "Adding some qualitative examples of how the models select examples will make it more intuitive to understand how EVIC works", I was mainly hoping to see some actual text examples so that I can have a more intuitive understanding about what example order does EVIC prefers. But you really don't have to include this in this rebuttal. It's not super critical and I'll be happy as long as you can include some examples in the final version.
**Res:** Thank you for your patient explanation. We will **accordingly include some examples in the final version** following your suggestions. As a demonstration, the examples we will include will be in the following format:
- *After warm-up training for Llama-3.1-8B, more than 83% of code and math samples are selected, but only 71.75% of general samples are selected. Which general samples are preferred by EVIC in the beginning of the training stage? We choose three general samples with the largest row sums and three general samples with the smallest row sums from the interaction matrix, as shown below. From their text, it can be observed that...*
- *In the second training iteration of Llama-3.1-8B, the coverage of math samples and general samples increases by 8.43% and 8.59%, respectively. However, the coverage of code samples increases by only 4.17%. Which code samples are newly selected in this stage by EVIC? We choose three code samples that are included in this iteration but not in the first iteration, as shown below. From their text, it can be observed that...*
- *After training for three iterations of Llama-3.1-8B, only 0.08% of the samples have never been selected, meaning they consistently conflict with the majority of samples. We sample three examples from them as follows. From their text, it can be observed that...*
- *More examples...*
Besides, we will also include some figures to show the frequency with which samples from different domains are selected, as illustrated in **Figure zLAH-1** to **Figure zLAH-8** in https://anonymous.4open.science/r/ICML25-EVIC-D5E8/zLAH.md. | null | null | null | null | null | null | null | null |
Differential Privacy Under Class Imbalance: Methods and Empirical Insights | Accept (poster) | Summary: This work looks at training classifiers with differential privacy (DP) guarantees in the presence of data imbalance (in the binary classification case) while enforcing fairness guarantees. They look at data augmentation methods and in-processing methods where fairness is attempted to be imposed by changing the model training process (viz. by using weights for different classes). It is seen that sophisticated private data augmentation methods (viz. GEM) tend to outdo in-processing based methods and certainly outperform non-private upsampling/oversampling methods. In addition, data augmentation needs to be done carefully and privately, as methods like oversampling or SMOTE can increase the sensitivity of the data due to dependence on existing minority samples.
Claims And Evidence: * The claims are supported by strong empirical evidence over binary classification tasks for different models for 8 datasets from imbalanced-learn and across multiple methods.
* Some claims about privacy are backed up by theoretical DP guarantees.
Methods And Evaluation Criteria: * Yes they do.
* However, the authors do not appear to use the same classifier architecture across all different methods, which concerns me as regards to the fairness of comparison.
Theoretical Claims: * The proofs seem correct, at least for the one on naive oversampling. I have not been through other proofs in detail.
Experimental Designs Or Analyses: * I think there's only one issue, that is with the heterogeneity of model types/architectures used for comparing different methods, as discussed in "Methods and Evaluation Criteria". It might be that this is a solid evaluation, but I need to understand the authors' choice of using different models for different methods better: 1) Why did they decide to use different models (XGBoost, logistic regression, FTTransformer)? What influenced their choices? Is this really an apples-to-apples comparison? 2) What may change if they use the exact same classifier across privacy-addition methods, so to speak?
Supplementary Material: I did not go through the supplementary material in detail, and just skimmed it. However, as Algorithm 3 is key to the discussion in the main text, I spent some time on it.
Relation To Broader Scientific Literature: * This supplements previous work on fairness in terms of utility and privacy (viz. Tran et al.) and works on alleviating data imbalance (viz. SMOTE), including by generating synthetic data with DP (viz. GEM, PrivBayes), in the context of machine learning, and contributes in terms of studying the efficacy of data processing or in-processing as a way of imposing fairness requirements. This investigation is timely and important as practitioners may benefit from studying the efficacy of these methods in terms of balancing fairness and privacy guarantees while maintaining utility.
Essential References Not Discussed: No missing references come to mind.
Other Strengths And Weaknesses: * Please refer to aforementioned comments. I think this paper has many strengths and provides a nice overview of using fairness-aware DPML methods to practitioners.
* However, one big weakness (potentially) is the heterogeneity of the classifier types used in the evaluation, which potentially is not an apples-to-apples comparison between the methods discussed in the paper.
* One minor limitation, which the authors acknowledge (and should not be held too strongly against them) is that their discussion and evaluation is limited to binary classification. However, it will be appreciated if the authors can provide a few more insights on generalizing it to the multiclass setting, beyond what is discussed in the paper.
Other Comments Or Suggestions: None.
Questions For Authors: * Can the authors please run experiments over all the methods that they discuss but compare over the same architecture for a better apples-to-apples comparison? This alone, if addressed, will be sufficient for me to raise my score.
* Or can you please justify, very concretely, why it is valid and fair to have a comparison using different models for each method? I know that there might be some limitations (viz. bagging only being possible with certain architectures viz. XGBoost). However, could it be that there exists another compatible architecture which, if used, may lead to a different trend?
As such, with the heterogeneity between models, I cannot fully certify if the empirical takeaways are actually valid, because this does not seem like an apples-to-apples comparison. What would help is if these trends are seen while using the **same** model across all these methods.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > **…limited to binary classification…insights on generalizing to the multiclass setting?**
Thank you for this interesting direction for extending our work; many of our results do extend naturally to multi-class settings. We’ll update our revised paper with an expanded version of the following:
**For SMOTE Result:** In both Proposition 4 and Theorem 5, the term $\left\lceil\frac{N}{n_1}\right\rceil$ reflects the number of iterations needed over the minority samples (with $N$ additional samples generated and $n_1$ original minority instances). In a multiclass setting with \(c\) classes -- each with $n_1, \dots, n_c$ samples -- we can simply apply the procedure independently for each class. For class $i$, one generates $N_i$ synthetic samples so that the iteration term becomes $\left\lceil\frac{N_i}{n_i}\right\rceil.$ Taking the worst-case over classes, i.e., $\max_{i \in [c]}\left\lceil\frac{N_i}{n_i}\right\rceil,$ ensures that the overall privacy analysis carries over directly.
**For ERM / DP-SGD:** Multinomial logistic regression and categorical cross-entropy loss (soft-max loss) are natural extensions of the binary setting to multi-class with these models. The loss (softmax with cross-entropy) is convex and differentiable with respect to the model parameters, so the sensitivity bounds used in our weighted ERM analysis hold -- with appropriate adjustments to account for the gradient computed over **all** classes.
**For GEM / Other Synthetic Data:**
Extending the DP synthetic data generation methods like GEM to multiclass settings is also straightforward! In the multiclass case, the generator is trained to learn the joint distribution over all variables, including a target variable that is potentially categorical.
> **...please justify why it is valid/fair to compare using different models for each method?**
Thank you for raising this point. In the revised paper, we will clarify the driving question of our work, and add a version of the following discussion to address your concerns.
Our work could be framed as a first step to answering the question: **Given that you want to make predictions using sensitive, class-imbalanced data, for a fixed privacy budget, which differentially private approach will give you the best performance?** We are not aware (as noted by Reviewer uyZY) of any other work that directly attacks this question.
These comparisons were inherently limited by the availability of DP algorithms with explicit adaptations under class imbalance (for example, we went to great lengths to construct a weighted the DP-ERM algorithm, see Theorem 5, Lemma 14 and the proofs, etc. in Appendix C.3.1).
Then, within each approach *variant* (disparate approaches both in pre-processing and in-processing), we selected candidates for highlighted comparison:
1. **Most performant pre-processing methods (GEM, DP Synthetic Data)**:
We use DP synthetic data approaches (GEM and PrivBayes) to generate a class balanced, synthetic dataset. This decoupling allowed us to use any strong non-private classifier downstream. We chose XGBoost precisely because it is known for its robust performance on imbalanced data, and when tested in the non-private setting (see Appendix E.2) we found it generally outperformed a logistic regression baseline (as expected). We made a point to highlight that (strong private data synthesizer)+(strong non-private downstream classifier) is a promising framework; evaluating just that class of models could be its own follow-up work.
2. **Most performant in-processing methods (Weighted ERM and DP-SGD with FTTransformer)**:
These methods are representative of, respectively, a private convex optimizer (for ERM) and a DP-SGD-trained neural architecture. Again, we needed to adapt an ERM algorithm under class imbalance. We believe adapting other private in-processing approaches under class imbalance is a very interesting direction for future work; however, it is not often straightforward due to particular care required in the privacy analysis for the sensitivity adjustment under weights.
We did not highlight the empirical comparisons for SMOTE and for bagging (both private and non-private), as they performed poorly and reduced the clarity of our takeaways for the most performant methods we evaluated.
In summary, we acknowledge that its worth carefully considering the appropriateness of assessing methods *across* model families, and appreciate your concern here. Our intent with this paper was to highlight the trade-offs that arise when addressing class imbalance under DP, and provide a study that covered a lot of ground. We’d further like to highlight that the heterogeneity in approach mirrors trends in prior work, where methods are often compared at fixed privacy budgets, in their most effective form, rather than compared within a uniform model class [e.g., Jayaraman et al. 2019, https://arxiv.org/abs/1902.08874 or Suriyakumar et al., 2021 https://arxiv.org/pdf/2010.06667 ).
---
Rebuttal Comment 1.1:
Comment: Dear authors, thank you so much for your rebuttal and your detailed answers.
I stand convinced of your first response, and I appreciate the thoroughness of it. As for the second, and I had to spend some time thinking about this because I appreciate your thorough response but struggled with how convinced I was with it: I understand the limitations, but to answer precisely the question you have framed up there, I am still not convinced that saying "using DP method X with model A outperforms DP method Y with model B, therefore, DP method A is better" is correct. It may be, but unless the authors use either the same methods or a well-justified metric that brings all of them on a level playing field, I am afraid I am not convinced by this argument, for a comparative study. It does, to an extent, answer, what is the "best" we can do with DP method "X" as compared to "Y", but that is not exactly the same question in my mind.
Therefore, I'll have to retain my score. I am, however, open to discussion.
---
Reply to Comment 1.1.1:
Comment: **We’re glad that you appreciated our response on multi-class generalization;** we were pleased to have an opportunity to consider it and add a discussion in the revised paper.
We understand your hesitation around our central comparative evaluation strategy; as you put it, you’re still not sure that "Using DP method X with model A outperforms DP method Y with model B, therefore, DP method X is better" is the right way to compare methods.
*We believe it would be helpful to reframe the structure of our comparison, to motivate why the comparative structure we chose was natural, meaningful and practically motivated.* We do this in with following 3 points:
**1. What Are We Comparing? Unit of Comparison Is a Pipeline, Not a Model:**
In the presence of both class imbalance and privacy constraints, privacy-preserving methods are rarely deployed in isolation from downstream modeling choices. That is, differential privacy is not a plug-in property -- it can interact with data characteristics, model class/architecture and optimization choices. Therefore, we argue that the natural unit of evaluation is the full learning pipeline -- from DP mechanism to model class to optimization procedure.
To be clear about what we mean by a “learning pipeline,” we’ll define the triple $(A, M, f)$, where:
1. $A$: the DP algorithm (e.g., GEM, DP-SGD, weighted DP-ERM, pre-processing steps that incur privacy loss, etc.)
2. $M$: the intermediate representation or data output (e.g., synthetic dataset, private gradients)
3. $f$: the final prediction function (e.g., XGBoost, logistic regression)
Our comparisons then ask: **Given a fixed privacy budget $\epsilon$, and a practical goal of maximizing predictive performance on imbalanced data, which pipeline $(A, M, f)$ yields the best results?**
We argue that this question is natural and important, because it reflects how DP methods are actually deployed: with tailored architectures and loss designs best suited to a level of privacy, data context and type of privacy mechanism used.
**2. Conversely, A Uniform Architecture May Undermine the Validity of the Comparison:**
We fully agree that "all else equal" comparisons (same architecture across multiple approaches to ensuring DP) are valuable for isolating specific effects. But here, enforcing architectural uniformity across fundamentally different DP techniques would introduce distortion:
1. Synthetic data methods (e.g., GEM) produce tabular data that can be passed to **any model.** GEM tends to perform best when paired with tree-based learners (which are known to perform well on tabular data), so it’s natural to use them downstream. However, we would be happy to add results comparing GEM+XGBoost with GEM+NonPrivLogReg and GEM+NonPrivFTTransformer if this would help address your concerns.
2. (Weighted) DP-SGD is designed and used with deep neural models in mind. Running (weighted) DP-SGD to update a model like logistic regression would likely not perform well at all, but we could try it if the comparison would alleviate some of the problems you see.
3. Similarly, the weighted ERM-based method targets convex losses under stronger (linear) model class assumptions, but this means we can conduct a more in depth privacy analysis.
In summary, we argue that using the same architecture across all methods risks favoring some methods and punishing others. By contrast, our approach chooses the most appropriate and representative model for each method family, at **pipeline** scale of comparison
**3. Standards from Prior Work**
Our evaluation framework aligns with some precedents set by prior work in the DP literature. For example, as we noted previously, [Jayaraman et al. 2019] and [Suriyakumar et al. 2021] both compare multiple DP methods under their most effective training pipelines, not just under a uniform model architecture. Our goal is not to isolate architecture as a variable, but to ask: Which end-to-end strategy works best for private imbalanced learning? We believe this is a natural question to ask, especially as we conduct this initial study that tries to cover a lot of ground on DP and imbalance learning.
**Your point is well taken though:** in our revised paper, we will clarify this evaluation philosophy. **We will also explicitly communicate that our empirical takeaways are on the scale of method+architecture pipelines** -- not about variations/nuances on the model classes in isolation (e.g. which architecture is best for weighted DP-SGD? etc.) which will require further exploration in future work.
We hope that this can address your concerns about the fairness of comparison. Thanks for engaging in the rebuttal phase, we appreciate your thoughts and feedback. | Summary: This paper studies the problem of privacy when the dataset is imbalanced such that there is one class that has significantly less data points than the other class. Specifically, the paper tackles the problem of training a binary classifier on imbalanced data. Known techniques for up-sampling the minority class data samples are studied and compared, while discussing the shortcomings and advantages of each. This was also shown experimentally.
## update after rebuttal
The authors have shed more light to their contribution; therefore, I raised my score to a 3.
Claims And Evidence: The paper supports the claims well with experiments.
Methods And Evaluation Criteria: The methods to evaluate the results are valid and they use real datasets, which is very good to show the real implications of this problem and different techniques.
Theoretical Claims: Although the work is mostly empirical, there are some propositions, lemmas, and theorems. Mainly, the proofs are in the appendix. I checked the correctness to the best of my ability, and I did not find any issues.
Experimental Designs Or Analyses: The experiments were designed well to support the claims of the paper. The comparisons done between the different private up-sampling techniques and their effect on the accuracy of the model supported the claims made in the paper.
Supplementary Material: I reviewed the proofs and the analyses.
Relation To Broader Scientific Literature: This work offers a good overview and comparison of the different techniques that could be used when the data is imbalanced. This would be helpful in some areas, such as medicine, where data could be very skewed.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper is very well written and easy to read and follow. However, my main issue with the paper is the originality. The paper uses different known techniques and compares them while giving some insights about them. I think this work is incremental despite offering a nice overview on the topic. I would recommend another venue for this work.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > **The paper is very well written and easy to read and follow.**
Thank you for your positive feedback regarding the clarity and readability of our paper. We spent a lot of time considering how best to present the nuances of this particular classification setting, and so appreciate this recognition.
> **However, my main issue with the paper is the originality. The paper uses different known techniques and compares them while giving some insights about them. I think this work is incremental despite offering a nice overview on the topic.**
We respectfully disagree; we believe ICML is the right venue for this work. Our paper builds on established imbalanced learning techniques and standard DP mechanisms, and it is, to the best of our knowledge, the first comprehensive study that systematically investigates differential privacy under class imbalance. We acknowledge that we evaluate class-imbalanced adaptations of pre-existing methods; however, this work is quite involved, and crucial to answering the questions our paper poses. We highlight several contributions, including:
**(1)** We rigorously show that well-known methods such as SMOTE and non-private bagging -- techniques that have been successfully applied in non-private imbalanced classification settings -- can dramatically inflate the sensitivity / render privacy guarantees meaningless when directly applied under DP.
**(2)** We introduce a weighted variant of the canonical private ERM approach, filling a notable gap in prior work (Theorem 5, see Lemma 14 and Section C.3.1 for the extensive necessary adjustments to show privacy).
**(3)** Our extensive empirical study -- across multiple imbalanced datasets and a range of privacy budgets -- is the “first work to extensively study the class-imbalance setting under DP” as noted by Reviewer uyZY. Our results not only demonstrate the limitations of certain approaches but highlight promising methods like DP synthetic data (via GEM) as (pre-processing) and the weighted ERM approach (as in-processing). | Summary: This paper deals with the (in)consistency of differential privacy and imbalanced class learning, especially binary classification problem where the minority class is very small. The non-private learning algorithms for the imbalanced classes usually increase the weights of minority classes through oversampling, argumentation, Bagging, reweighting methods etc. However, these methods are shown to be inconsistent with differential privacy because DP would increase the privacy risk, bias and unfairness. So this paper evaluated the private versions of these methods and provide some suggestions.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: not all of them. I checked some essential ones and those in Section 3. They are correct.
Experimental Designs Or Analyses: yes. The experiments are well-designed
Supplementary Material: I checked the materials especially the part related to DP-SGD
Relation To Broader Scientific Literature: This paper helps better understand the relationship between differential privacy and those standard learning algorithms for imbalance classes. It seems that it is related to invidualized differential privacy in the literature, which is not discussed in the paper.
Essential References Not Discussed: no as far as I know
Other Strengths And Weaknesses: Strengths:
(1) The paper provided a systemetic evaluation of different differential private algorithms used in the standard machine learning for imbalanced classes. The observations are interesting and convincing.
(2)The paper tackles an interesting and important problem in practice.
Weakness:
(1) The abstract says this work"formalizes these challenges". But I did not find such a formalization. Also the abstract says that this paper "provides a number of algorithmic solutions". I could not find those solutions in the paper. My impression is that this paper mainly focus on the evaluation of the DP version of those learning algorithms for imbalanced learning not on the methods.
(2) The presentation is a little sloppy. Moreover, different parts seems to be isolated from each other. There are many propisitions in this paper. It seems that they are just flattened. I don't know which one is the central and main proposition.
(3) Proposition 2 is trivial. It is an easy observation.
(4) Theorem 5 is very confusing. There are no explicit intuition before this proposition.
(5) Algorithm deals with multi-label classification inAlgorithm 1 instead of binary classification problem as specified in Introduction.
Other Comments Or Suggestions: (1) Line 85: undersampling -> subsampling
(2) Line 152: L2->L_2
Questions For Authors: Q1: In the last senetence of the first paragraph in Introduction, "these methods ... assume that false positives and false negatives have equal misclassification costs". What does this mean?
Q2: Could you explain more about the privacy loss scale in Lines 78-80?
Q3: Could you explain Line 6 inAlgorithm 1?
Q4: Could you explain the reason why "Re-weighting of samples in the loss function pre-clipping does not affect these privacy
guarantees" (Line 1795)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: > **...related to invidualized differential privacy, not discussed...**
We thank the reviewer for raising this point. While our sensitivity analysis -- specifically, how certain samples in imbalanced datasets incur higher privacy loss -- echoes themes from individualized/personalized DP, our work is rooted in standard, global worst-case DP. We will add a brief discussion in the revised version to clarify the connection.
> **(W1) ...did not find a formalization / could not find solutions...**
A fully general formalization of the challenges in DP imbalanced classification is difficult without strong distributional assumptions. Instead, we formalize key sub-problems. For example, Theorem 3 and Proposition 4 characterize the SMOTE and bagging approaches under class imbalance, and Example 11 with Proposition 12 (deferred to the Appendix) does so under a Gaussian mixture assumption. We would be happy to revise from "formalizes these challenges" to more precisely stating that we formalize "approach-specific challenges."
Our solutions include both theoretical insights and concrete algorithmic adaptations. For example, we introduce a private weighted DP-ERM algorithm (Algorithm 1, Theorem 5) and analyze DP-SGD with weighted cross-entropy (Proposition 6, Lemma 19). We also propose a class-conditional sampling pre-processing approach with private synthetic data (Algorithm 3) and provide extensive empirical evaluations. We’d be happy to also adjust the language to clarify these claims.
> **(W2)...didn't know what was central and main proposition...**
Our work does not have a single central theorem; instead, we compare a variety of methodologies for imbalanced classification under differential privacy constraints.
> **(W3)...Proposition 2 trivial...**
We agree, Proposition 2 (regarding the sensitivity amplification via oversampling) is straightforward. We wanted to formalize this intuitive observation to set the stage for the more complex sensitivity analysis in the SMOTE setting (Theorem 5, see Appendix B.1 for proof). We’d be happy to present it informally, inline, so that the central contributions remain emphasized.
> **(W4)...Theorem 5 is confusing...**
Due to space constraints, we deferred much of the discussion and setup for Theorem 5 to Appendix C.3 (in particular, see the paragraph titled “Notation for ERM Proof” and the subsequent Lemma 14, which accounts for the main sensitivity adjustment for weights for privacy). In short, Theorem 5 shows that Algorithm 5 is differentially private. The two paragraphs preceding Theorem 5 respectively provide **(1)** the notation with discussion of weights, and **(2)** intuition for how the weights play a role in the proof. We'd be happy to move anything from Appendix C.3 back into the body to make this result more clear.
> **(W5) (typos)**
Thank you for catching the typos - we will correct them in the revised version (e.g., adjust Line 1 in the Algorithm so that $y_i \in \\{0,~1\\}$)
> **(Q1) [what do we mean by assuming that FP and FN have equal misclassification costs]?**
This refers to the common design assumption that the cost of a false positive is identical to that of a false negative. For many applications where imbalanced learning commonly arises, this assumption doesn’t hold. For example, in detecting rare cancers or financial fraud, missing a rare but critical positive event (false negative) might be far more consequential than a false alarm.
> **(Q2)...privacy loss scale in Lines 78-80?**
Certainly. In those lines, we briefly summarize how SMOTE can drastically increase the sensitivity of a downstream DP algorithm. Specifically, by generating multiple synthetic points from a single minority example, the effective privacy parameter $\epsilon$ is scaled by a factor that is exponential in the data dimension and linear in the number of synthetic points. This means that even if the base algorithm is $\epsilon$-DP, applying SMOTE without proper adjustments as a pre-processing step may lead to an effective privacy loss ($\epsilon’$) that is substantially higher. See e.g., the scaling and reverse-scaling we give in Table 2.
> **(Q3) Line 6 in Algorithm 1**
Line 6 describes the core optimization of the weighted DP-ERM algorithm: minimizing the weighted empirical risk, which combines the per-sample loss (weighted by class frequency), an objective perturbation noise term, and a regularizer. We would be happy to elaborate on this step (and provide references for its standard use) in the final version for added clarity.
> **(Q4) (explain Line 1795)?**
The privacy guarantees in our algorithm are based on the sensitivity of the per-sample gradient, which is controlled by a clipping step that bounds the norm of each gradient to a fixed constant C. Although re-weighting changes the magnitude of the computed gradients, the subsequent clipping ensures that no individual sample's contribution exceeds C. Thus, the overall sensitivity remains unchanged. | Summary: The paper explores class imbalance in differentially private ML settings. The authors consider common pre-processing and in-processing methods for dealing with class imbalance, and look at extending them to the DP setting. They show that some commonly used non-private methods like SMOTE are not well suited to the DP setting and that alternatives like DP synthetic data or DP-weighted ERM perform better in a private class imbalance setting. Experiments are performed over 8 benchmark imbalanced binary classification datasets.
Claims And Evidence: The paper generally make two main claims:
1. The first claim is that oversampling methods are poor for DP settings as they increase the sensitivity of DP algorithms that are trained on them. This is supported by clear theorems that show the sensitivity is amplified and these approaches are not well-suited.
2. The second is that the use of DP synthetic data is the strongest approach for dealing with class-imbalance. This is fairly well-supported by an extensive set of experiments, although some results I feel are misleading or unclear (see weaknesses + questions below).
Methods And Evaluation Criteria: The methods and evaluation criteria used are suitably chosen for the problem and are fairly exhaustive. The paper considers a good number of methods for dealing with class imbalance (as highlighted in Table 1) and how to extend them to a DP setting. Experiments are performed over 8 commonly used benchmark datasets in imbalanced binary classification problems and multiple evaluation metrics are presented for the classifiers.
Theoretical Claims: I did not review the full technical proofs (contained in the appendix) but the stated results in the main paper seem to logically follow.
Experimental Designs Or Analyses: The experimental design is generally sound. The methods are ranked across 8 benchmark datasets for imbalanced data and a specific dataset is chosen to highlight multiple evaluation metrics across the methods. However, I have a few issues with the setup used for GEM (see questions below).
Supplementary Material: The supplementary material contains full technical details and proofs of the privacy guarantees of the methods proposed in the main paper along with the full experimental results across each of the 8 benchmark datasets which replicates plots presented in the main paper but to other datasets.
Relation To Broader Scientific Literature: The key contributions fit well into the broader literature on DP-ERM and private synthetic data generation and as far as I am aware, these methods have not been studied extensively in class-imbalance settings. To the best of my knowledge, this is also the first work to extensively study the class-imbalance setting under DP.
Essential References Not Discussed: There are no related works that I feel are missing or not discussed.
Other Strengths And Weaknesses: **Strengths:**
- Class imbalance in a DP setting is an important practical problem that has many uses yet is not well-studied in the literature. This paper addresses and fills this research gap.
- The paper covers a wide-range of class imbalance methods for both pre-processing and in-processing and shows how to extend them to the DP setting. The experiments are also extensive and show a clear conclusion that DP synthetic data is the most robust method.
- The paper is well-written and generally clear.
**Weaknesses:**
- The results are limited to binary classification settings and it is not immediately clear how findings or some methods can be extended to a multi-class setting.
- The leading conclusion is that DP synthetic data is a strong option to handle class imbalance, however the evaluation against other baselines seems unfair (see below).
- I think SMOTE presented as is, is also an unfair baseline (see questions below).
Other Comments Or Suggestions: N/A
Questions For Authors: 1. The GEM+XGBoost method is misleading because it is compared against (mostly) logistic regression baselines. It is unclear from Table 3 how much of the benefit comes from the DP synthetic data or if the benefit is from the actual XGBoost model vs. the simpler logistic regression models. Why was XGBoost chosen instead of using GEM+LogReg? Indeed, some of the tables in the Appendix for the non-private setting highlight that there is often a big accuracy discrepancy between (non-private) LogReg and XGBoost and this would also be reflected in the DP experiments.
2. The comparison for SMOTE seems somewhat unfair. As stated, using SMOTE as-is increases the DP sensitivity which in turn amplifies the DP epsilon needed to maintain the same level of DP which is a nice result. However, the actual SMOTE algorithm has not been adapted for privacy compared to other methods specifically changed to provide DP guarantees. Do you see natural extensions to SMOTE that are privacy-friendly, i.e., by perturbing points that are sampled?
3. How can the leading methods be extended to multiclass settings? It’s briefly discussed for the oversampling methods like SMOTE, but do the methods like synthetic data and weighted ERM easily extend?
4. For GEM, it is unclear to me if rejection sampling was used or conditional sampling? If conditional sampling, was the generator network structure changed over the standard GEM approach?
5. Was any of the GEM training procedure changed to adapt to a class-imbalanced setting? More specifically, for the workload of queries given to GEM, do you have suggestions for achieving best accuracy in imbalanced settings?
6. To clarify in L340, I presume $B$ in the $2C/B$ refers to the DP-SGD minibatch size? I am not sure this is clear from the main paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: > **(Q1) Why XGBoost instead of using GEM+LogReg?**
Thank you for your comment, hopefully we can clarify our choices here. Our primary goal was to compare general approaches to handling imbalanced classification under differential privacy -- not necessarily to benchmark model families (e.g., logistic regression vs. XGBoost, etc.). In our setup, we tested GEM and PrivBayes as differentially private pre‐processing steps to generate a balanced, synthetic dataset. This approach decouples the rebalancing from the classifier so that we can use any strong non-private model downstream, as we know that private ERM (regression) methods have performance limitations [e.g., Jayaraman et al. 2019, https://arxiv.org/abs/1902.08874]. Then, we chose XGBoost because this is the choice that a practitioner would likely make due to its well known overall performance, and in particular its robustness on imbalanced datasets.
However, you are correct that, although a non-private XGBoost model will generally outperform non-private logistic regression, in some of our non-private experiments in Appendix E.2 the LogReg method slightly outperformed XGBoost. However, in our private experiments, we found that the GEM+XGBoost approach was more robust to noise introduced in the dataset for privacy. We’d be happy to add these experiments on the performance of the GEM+LogReg approach into the final version of our paper. However, we stress that our aim generally was to illustrate that leveraging DP synthetic data enables the use of state-of-the-art non-private classifiers, and that (strong private data synthesizer)+(strong non-private downstream classifier) is a promising approach.
> **(Q2) Do you see natural extensions to SMOTE that are privacy-friendly...?**
Thank you for bringing this up; as part of this work, we did spend time considering how one might develop a differentially private SMOTE algorithm. However, in our analysis for Theorem 3, we showed that SMOTE’s linear interpolation approach makes it inherently very sensitive (i.e., its sensitivity grows exponentially with the data dimension and linearly with the number of synthetic samples). In other words, even if one were to add noise directly to the interpolated points (with a differentially private additive noise mechanism), the resulting privacy loss would be unacceptably high. We view this as a key challenge: the reliance on the precise locations of pairs of minority points renders a direct privatization of SMOTE impractical.
Instead, our analysis of SMOTE motivated us to leverage established DP synthetic data methods based on the ``Select–Measure–Project’’ paradigm. These methods learn a DP approximation of the underlying data distribution and then generates synthetic samples in a way that avoids the high sensitivity pitfalls of linear interpolation (by relying on less sensitive $k$-way marginal measurements). So, in summary, our results suggest that using DP synthetic data generation methods circumvents linear interpolation between minority examples in the data (which we showed was highly sensitive, making a direct differentially private adaptation of SMOTE impractical).
> **(Q3)...How can the leading methods be extended to multiclass settings?**
Thank you for this interesting direction for extending our work! **Please see our response to *Reviewer PW3A*, who also asked for a discussion of this extension.**
> **(Q4)...rejection sampling or conditional sampling (GEM)**
In our experiments we adopted a conditional sampling strategy -- this is sample efficient and directly addresses class imbalance. Importantly, the underlying generator network structure remains unchanged relative to the standard GEM approach. We will make this more clear in the final version of the paper.
> **(Q5)...was any of the GEM training procedure changed?**
No substantial changes were made to the core training procedure of GEM itself. Our approach leverages the standard GEM training protocol; the adaptation to handle imbalance is performed at the sampling stage. We view this as a feature, since practitioners would not have to change their training procedures to accommodate imbalanced data. Regarding the workload of queries (i.e., the set of measurements used during synthetic data generation), our experiments relied on the default $k$-way marginal selection. That said, in general we believe that selecting queries that capture the most informative low-dimensional marginals -- especially those relevant to the class imbalance itself -- could potentially improve performance in imbalanced settings. This is an interesting direction for future work, and we will add a discussion on it in the final version, thank you.
> **(Q6)...DP-SGD minibatch size clarification.**
Apologies, that did not make it up from the statement of Lemma 19 in the Appendix, but yes, that is correct, B denotes the DP-SGD minibatch size. We will make sure to state this in the final version, thank you!
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their response. I feel most of my questions have been adequately addressed and I have raised my score to a 4.
However, I strongly encourage the authors to include results on GEM+LogReg in a revised version (whilst still keeping GEM+XGBoost) to give a data point for a more uniform comparison. I have read the discussion with Reviewer PW3A and feel the argument about studying methods as a combined pipeline is valid (i.e., an advantage of DP-SDG is it can be used with any model), but still feel strongly there should at least be some initial experiments where GEM+LogReg is compared.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer uyZY,
We're pleased that our response addressed many of your concerns, and that you took the time to review our discussion with Reviewer PW3A and found it convincing. We will add results on GEM+LogReg in the revised version of the paper, as requested.
Thank you again for taking the time to engage with us during this rebuttal phase! | null | null | null | null | null | null |
RepLoRA: Reparameterizing Low-rank Adaptation via the Perspective of Mixture of Experts | Accept (poster) | Summary: This work studies a new variant of LoRA. First, the authors show that under certain settings, LoRA requires exponential sample complexity. Then, they introduce a simple reparameterization strategy, which builds a single generator for Q, V layers. The generator can be a single layer with or without activations. Using this reparameterization, the authors show that the sample complexity can be reduced to polynomial scale, which reveals the advantage of the new method. Experiments are conducted on multiple domains including LLMs, images/videos and multi-modal datasets. The proposed method consistently outperforms LoRA.
## Update after rebuttal
As the authors' address most concerns of all reviewers, I would keep the score.
Claims And Evidence: Yes, the claims are supported by theoretical and empirical analysis.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I did not check the proof.
Experimental Designs Or Analyses: The experimental design is sound, including datasets and pre-trained models of different domains.
Supplementary Material: I checked Section C and D in the appendix.
Relation To Broader Scientific Literature: The key contribution is to improve LoRA by reparameterization. It may contribute to the field of parameter-efficient fine-tuning, including many other variants of LoRA.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: ### Strengths
1. This work studies LoRA from the view of MoE, and theoretical analysis about the sample complexity. These results may be useful for future research in this field.
2. The proposed method is simple and theoretically sound. It may be also applied to other variants of LoRA.
3. Experiments are also conducted on diverse domains. The proposed method seems good.
### Weakness
1. While the method is simple and advantageous over LoRA, it would be better to compare with some more advanced variants of LoRA, especially some work that applies hypernetworks to generate adapters, which is very similar to this one. For example the following.
https://openreview.net/forum?id=iP8ig954Uz
2. The parameters of RepLoRA are higher than LoRA. Did the authors try experiments with comparable parameter sizes?
Other Comments Or Suggestions: In Line 349, PETL is not introduced.
Questions For Authors: See above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the feedback and would like to address the concerns as follows:
+ **Regarding the comparison with other variants of LoRA:** Following the reviewer’s suggestion, we conducted an additional experiment on the image classification task using the FGVC dataset to compare RepLoRA with VeRA [1] and DoRA [2]. The results are presented below:
| Methods | CUB-200-2011 | NABirds | Oxford Flowers | Stanford Dogs | Stanford Cars | AVG | PPT |
| -------- | -------- | -------- | -------- | -------- | -------- | -------- | -------- |
| LoRA | 84.6 | 78.2 |98.9 | 85.1 | 77.1 |84.8 | 0.82 |
| DoRA | 87.3 | 80.0 |99.1 | 87.6 | 81.9 |87.2 |0.88 |
| VeRA | 85.1 | 79.2 |97.4 | 87.3 | 76.3 |85.1 |0.88 |
| RepLoRA | **89.1** | **86.1** | **99.3** | **91.2** | **87.6** | **90.7** |**0.90** |
Furthermore, we would like to highlight that RepLoRA has already been compared to other methods that utilize hypernetworks to generate adapters in the main paper. Specifically, in the main text, we included a comparison with prefix tuning [3], which leverages an MLP to generate the adapters, specifically the prepended prompts. Building on the reviewer’s helpful suggestion, we will also incorporate comparisons with VeRA and DoRA in the revised version to provide a more comprehensive evaluation.
+ **Regarding the comparisons with comparable parameter sizes:** In all experiments, we reparameterized the low-rank adapters using MLPs with a hidden dimension of $h=64$, which we identified as the optimal setting through extensive tuning in terms of both PPT and accuracy. To address this concern, we also conducted experiments with a reduced hidden dimension of $h=8$, resulting in a comparable parameter size. The results, presented below, show a slight overall drop; however, RepLoRA still significantly outperforms vanilla LoRA, demonstrating its robustness and practical benefits under tighter parameter constraints:
| Methods | CUB-200-2011 | NABirds | Oxford Flowers | Stanford Dogs | Stanford Cars | AVG | PPT |
| -------- | -------- | -------- | -------- | -------- | -------- | -------- | -------- |
| LoRA | 84.6 | 78.2 |98.9 | 85.1 | 77.1 |84.8 | 0.82 |
| RepLoRA $(h=8)$ | 87.5 | 85.8 |98.4 | **91.6** | 83.0 | 89.2 |0.90 |
| RepLoRA $(h=64)$ | **89.1** | **86.1** | **99.3** | 91.2 | **87.6** | **90.7** |**0.90** |
Following the reviewer's suggestion, we will include this finding in the appendix of the final manuscript.
**References**
[1] VeRA: Vector-based Random Matrix Adaptation. ICLR. 2024
[2] DoRA: Weight-Decomposed Low-Rank Adaptation. ICML. 2024
[3] Prefix-Tuning: Optimizing Continuous Prompts for Generation. ACL. 2021
---
Rebuttal Comment 1.1:
Comment: Thanks for the authors' response. Most of my concerns are addressed. I would keep the score.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer ykAM,
We are glad to hear that our response addresses your concerns, and we would like to thank you so much for keeping the positive rating of 4 (Accept), which we really appreciate. If you have any further concerns, please feel free to let us know. We will keep revising the manuscript based on the feedback from you and other reviewers.
Thank you,
The Authors | Summary: The authors proposed two reparametrizations of LoRA under which the convergence rate improves from $\mathcal{O}_P(\frac{1}{\log^{\tau}(n)})$ of vanilla LoRA to $\mathcal{O}_P(\sqrt{\frac{\log (n)}{n}})$. Empirical results demonstrate that both reparametrizations outperform vanilla LoRA on real datasets.
Claims And Evidence: The claim that the proposed reparametrizations are more sample efficient are backed up by formal theorem statements and their proofs. However, there is a discrepancy between the theoretical results and the experimental setup: while Theorems 4.1-3 assume $A_Q$ and $A_V$ are tied, the experiments only assume that they result from the same low rank matrices. Therefore the theoretical results cannot fully explain the empirical successes.
Methods And Evaluation Criteria: The experiment setup seems correct. However, I would love to see experiments that validate the theoretical results: namely experiments that tie $A_Q$ and $A_V$ together.
Theoretical Claims: I checked proof for Theorem 4.1 which seems correct. However the implications in L187-196 (right column) should be formalized into a proposition and proven. I did not carefully check proofs for Theorems 4.2-3 which also appear in the appendix.
Experimental Designs Or Analyses: A main message of this paper is that parameter estimation of the proposed reparameterizations is much more sample efficient. Besides the discrepancy between what is being proven and what is being implemented, another issue is that the authors did not explicitly evaluate whether the reparametrization hurts expressiveness in real world tasks when data is abundant. One way to help answer this question is to evaluate on pretraining tasks where there is much more training data.
Supplementary Material: Yes. The proofs.
Relation To Broader Scientific Literature: This work adds on the ongoing discussion on how to best train LoRA models ([Yen et al., 2025](https://openreview.net/forum?id=VpWki1v2P8), [Hayou et al., 2024](https://arxiv.org/abs/2402.12354)).
Essential References Not Discussed: Discussion of previous empirical observations on LoRA's performance (_e.g._, [Biderman et al., 2024](https://arxiv.org/abs/2405.09673)) can further improve the paper.
Other Strengths And Weaknesses: This paper explores the sample efficiency aspects of LoRA which is a novel and significant contribution.
Other Comments Or Suggestions: - Minor editing errors on L218, L175 (right column), and L716.
- The paper is both dense and packed; proof sketches in the main text can provide useful guidance for the reader.
- Choice of nonlinearity function used is missing in the manuscript.
Questions For Authors: n/a
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the valuable feedback and would like to address the concerns raised as follows:
+ **Regarding the discrepancy between the theoretical results and the experiment setup**: Thanks for this feedback. We would like to clarify that the assumption in Section 4.2 that $A_Q=A_V$ is for simplicity and can totally be generalized to the setting where they share only the learnable matrix $A$. In particular, we can reformulate those matrices as $A_Q=W_{Q,1}A, A_V=W_{V,1}A$ for the simple linear reparametrization and as $A_Q=\sigma_1(W_{Q,1}A), A_V=\sigma_1(W_{V,1}A)$ for the non-linear reparametrization. Tailored to that setting, we need to add several additional terms involving parameters $W_{Q,1}$ and $W_{V,1}$ rather than merely parameters $W_{1}$ as in the current setting, making the convergence analysis unnecessarily complicated. Therefore, we assume without loss of generalization that $A_{Q}=A_{V}=W_{1}A$ or $A_{Q}=A_{V}=\sigma_1(W_{1}A)$ in Section 4.2 to simplify the analysis, making it more accessible.
+ **Regarding the experiment tying $A_Q$ and $A_V$:** To further support our theoretical findings, we conduct experiments on FGVC datasets by tying $A_Q$ with $A_V$ and $B_Q$ with $B_V$ in RepLoRA. The results, summarized in the table below, show that tying $A_Q$ and $A_V$ slightly reduces the model's expressiveness, resulting in a modest drop in performance compared to the original RepLoRA with untied matrices. However, tied RepLoRA still significantly outperforms vanilla LoRA, which reinforces the practical value of our approach, even under constrained parameterization.
| Methods | CUB-200-2011 | NABirds | Oxford Flowers | Stanford Dogs | Stanford Cars | AVG |
| -------- | -------- | -------- | -------- | -------- | -------- | -------- |
| LoRA | 84.6 | 78.2 |98.9 | 85.1 | 77.1 |84.8 |
| RepLoRA (tied) | 87.2 | 83.8 |99.0 | 85.6 | 85.4 |88.9 |
| RepLoRA (untied) | **89.1** | **86.1** | **99.3** | **91.2** | **87.6** | **90.7** |
+ **Regarding the implications of Theorem 4.1:** Thanks for your comment. We would like to emphasize that the results in lines 187-196 (right column) are consequences of Theorem 4.1 in our paper. In particular, by combining the result of Theorem 4.1 and the formulation of the Voronoi loss $\mathcal{D}_{1,r}$ in lines 167-173 (right column), we deduce the convergence rates of low-rank matrices estimation are slower than polynomial rates $O(n^{1-/2r})$ for all $r\geq 1$, where $n$ is the sample size. Due to the inequality $\log(n)<n$, these rates are even slower than the order $O(1/\log^{\tau}(n))$ for some positive constant $\tau$. As a result, to achieve a given approximation error $\epsilon=O(1/\log^{\tau}(n))$ of estimating the low-rank matrices, we need exponentially many data points $O(\exp(\epsilon^{-1/\tau}))$. We will consider formulating those implications into a corollary following Theorem 4.1 in the revision of our manuscript.
+ **Regarding the activation function**: The nonlinearity was implemented using the sigmoid function. We appreciate the reviewer’s suggestion and will include this detail in the final revision.
---
Rebuttal Comment 1.1:
Comment: Thank you for the response! I really appreciate the new parameter tying experiments.
Since a main message of this paper is the proposed affine reparametrization leads to better sample efficiency, I still think Thms 4.2 and 4.3 have to be modified to untie $A_Q$ and $A_V$, and similarly for $B_Q$ and $B_V$. The full proof can appear in the appendix in case there are space issues.
If the modification is too difficult, at the very least the authors should show a counter example where $\{A, B\}_Q$, $\{A, B\}_V$ are tied but sample complexity is still super polynomial.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer 8a5d,
Thank you so much for your response, which we really appreciate. **We would like to confirm that the results of Theorem 4.2 and Theorem 4.3 can totally be generalized to the setting where $A_Q,A_V$ are untied and $B_Q,B_V$ are untied without any technical issues**. Under that scenario, these matrices are formulated as
$A_Q=\sigma_1(W_{Q,1}A), A_V=\sigma_1(W_{V,1}A)$
and
$B_Q=\sigma_2(W_{Q,2}B), B_V=\sigma_2(W_{V,2}B)$
for the non-linear reparametrization setting. In response to these formulation changes, it is necessary to modify the Voronoi loss function $D_3(\tilde{G},\tilde{G}_{\ast})$ defined in lines 277-287 as *(we have to break down the loss formulation as the tex compiler does not allow us to type in full, we are really sorry for this inconvenience)*
$D_3(\tilde{G},\tilde{G}_{\ast})=$
$\sum_{j=1}^{L}\Big|\sum_{i\in\mathcal{V}_j}\exp(c_i)-\exp(c^{\ast}_j)\Big|$
$+\sum_{j:|\mathcal{V}_j|=1, i\in\mathcal{V}_j}\exp(c_i)$
$\Big(||\Delta (W_{V,2}B)_{ij}||$
$+||\Delta (W_{Q,1}A)_{ij}||$
$+||\Delta (W_{V,2}B)_{ij}|| $
$+||\Delta (W_{V,1}A)_{ij}\|\Big)$
$+\sum_{j:|\mathcal{V}_j|>1, i\in\mathcal{V}_j}\exp(c_i)$
$\Big(||\Delta (W_{V,2}B)_{ij}||^2$
$+||\Delta (W_{Q,1}A)_{ij}||^2$
$+||\Delta (W_{V,2}B)_{ij}||^2$
$+||\Delta (W_{V,1}A)_{ij}\|^2\Big).$
Then, by employing the same arguments as in Appendix A.3, we obtain the estimation rates of the low-rank matrices through the bound $D_3(\tilde{G}n,\tilde{G}_{\ast})$ as in Theorem 4.3. It can be seen that the convergence behavior of the low-rank matrix estimation remains unchanged compared to that in the current paper. Additionally, the result for the simple linear reparametrization (Theorem 4.2) can also be generalized analogously. Therefore, we simplify the presentation of the convergence analysis by tying $A_Q$ and $A_V$, $B_Q$ and $B_V$, which helps reduce several inessential terms in the Voronoi loss function. However, **as per your suggestion, we will consider modifying the settings of Theorem 4.2 and Theorem 4.3 as above and including respective proofs in the revision of our manuscript.**
Thank you,
The Authors | Summary: This paper proposes RepLoRA, a method that reparameterizes the low-rank matrices of LoRA using a lightweight MLP. RepLoRA surpasses baseline LoRA by up to 40.0% and achieves similar results with baseline with only 30.0% of the training data. Additionally, this work provides a theoretical analysis of LoRA from the perspective of a mixture of experts, demonstrating that reparameterization can reduce the data needed to achieve a desired estimation error from an exponential scale to a polynomial scale. Experiments across various tasks, including language (commonsense reasoning), image (classification), video (video action recognition), and multi-modal (image/video-text understanding), demonstrate the effectiveness of the proposed method.
Claims And Evidence: Most of the claims are supported by cited works.
Methods And Evaluation Criteria: The proposed method is effective and the evaluation criteria are valid.
Theoretical Claims: I cannot verify the correctness of the proofs due to my non-mathematical background. Please refer to other reviewers for the correctness check.
Experimental Designs Or Analyses: The experiments robustly demonstrate the effectiveness of the proposed method.
Supplementary Material: not provide.
Relation To Broader Scientific Literature: Low-rank Adaptation (LoRA) has gained significant traction as a method for fine-tuning large-scale foundation models, yet its theoretical underpinnings have remained relatively unexplored. This paper contributes to the broader scientific literature by providing a theoretical analysis of LoRA through its connection to Mixture of Experts models. By situating LoRA within this framework, they demonstrate that simple reparameterizations of LoRA matrices can significantly expedite the low-rank matrix estimation process. Specifically, the findings show that reparameterization can reduce the data required to achieve a desired estimation error from an exponential to a polynomial scale, thereby enhancing sample efficiency.
Essential References Not Discussed: Most of the relevant related works have already been cited.
Other Strengths And Weaknesses: Strengths
1.This work provides an insightful analysis of the impact of LoRA on multi-head self-attention layers from the perspective of a mixture of experts (MoE), offering valuable inspiration.
2.The proposed RepLoRA achieves outstanding results across various tasks, including commonsense reasoning, image classification, video action recognition, and image/video-text understanding.
Weaknesses
1.It would be better to provide experimental analysis for the theoritical proofs, such as the convergence curve w./w.o reparametrization.
2.Lack of comparison with similar works, such as [a,b,c]
[a] DoRA: Weight-Decomposed Low-Rank Adaptation
[b] VERA: VECTOR-BASED RANDOM MATRIX ADAPTATION.
[c] LORA-FA: MEMORY-EFFICIENT LOW-RANK ADAPTATION FOR LARGE LANGUAGE MODELS FINE-TUNING
Other Comments Or Suggestions: see Strengths And Weaknesses
Questions For Authors: see Strengths And Weaknesses
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the constructive feedback and would like to address your concerns as follows:
**Regarding the analysis of the theoretical results:** Our theoretical analysis demonstrates that LoRA with reparameterization offers superior *sample efficiency* compared to LoRA without reparameterization. To empirically analyze this theoretical claim, we dedicated the final experiment in the experimental section to validate these theoretical findings. The results show that reparameterization in LoRA significantly improves *sample efficiency*, as illustrated in Figure 2.
**Regarding the comparison with related works:** Following the reviewer’s suggestion, we have included additional comparisons with VeRA [1] and DoRA [2] on the image classification task using the FGVC dataset, as detailed below:
| Methods | CUB-200-2011 | NABirds | Oxford Flowers | Stanford Dogs | Stanford Cars | AVG | PPT |
| -------- | -------- | -------- | -------- | -------- | -------- | -------- | -------- |
| LoRA | 84.6 | 78.2 |98.9 | 85.1 | 77.1 |84.8 | 0.82 |
| DoRA | 87.3 | 80.0 |99.1 | 87.6 | 81.9 |87.2 |0.88 |
| VeRA | 85.1 | 79.2 |97.4 | 87.3 | 76.3 |85.1 |0.88 |
| RepLoRA | **89.1** | **86.1** | **99.3** | **91.2** | **87.6** | **90.7** |**0.90** |
The results demonstrate that RepLoRA outperforms both LoRA variants by large margins, emphasizing its practical advantages. In response to the reviewer’s suggestion, we will include this finding in the final revision.
**References**
[1] VeRA: Vector-based Random Matrix Adaptation. ICLR. 2024
[2] DoRA: Weight-Decomposed Low-Rank Adaptation. ICML. 2024 | Summary: The apper combines LoRA into multi-head parts of MSA and treats different heads as experts to build a mixtural of experts. In addition, authors use lightweight MLP to conduct reparameter opertations, which improves sampling efficiency while reducing data requirements compared to the original LoRA.
Claims And Evidence: The claims in the submission are generally well-supported.
Methods And Evaluation Criteria: The proposed method offers a novel insight, reducing the data needed to achieve a desired estimation error from an exponential
scale to a polynomial scale.
+ Authors measure classification accuracy trends at different training scales.
+ Linear and nonlinear RepLoRA modules are ablated on 7 application scenarios.
+ Based on the baseline LLama7B/13B, the proposed methods are verified to be effective on multiple datasets
Theoretical Claims: Theoretical proofs are provided. Based on it, authors discuss LoRA with MoE for achieving optimal sampling. Furthermore, RepLoRA was proposed with an effective and efficient approach to PEFT.
Experimental Designs Or Analyses: The experimental designs are comprehensive, with LLama7B/13B baselines and extensive datasets. By experimental analysis, the proposed methods are verified in both aspects in performance and parameters.
Supplementary Material: I have reviewed the supplementary material, but I cannot work out the proof details myself right now.
Relation To Broader Scientific Literature: This paper is closely related to the relevant research in fields of LoRA, MOE, and PEFT. If possible, authors can further illustrate the related mathematical basis/thinking in scientific literature.
Essential References Not Discussed: None
Other Strengths And Weaknesses: + Strengths
1) The proposed framework serves as a theoretical foundation that underpins the various methodologies and processes within LoRA scope.
2) Authors measure classification accuracy trends at different training scales.
3) Authors perform experiments on multiple scenarios for linear and non-linear RepLoRA modules.
4) LLama7B/13B are classical LLMs. The proposed methods utilize LLama7B/13B to verified to be effective on multiple datasets
- Weaknesses
1) The experimental situation with more LoRA adapters is unknown.
2) Should compare LoRA with MoE works [1, 2 , 3]
[1] Mixture-of-loras: An efficient multitask tuning for large language models. COLING. 2024.
[2] Mixture-of-subspaces in low-rank adaptation. EMNLP. 2024.
[3] MoR: Mixture of Ranks for Low-Rank Adaptation Tuning. Arxiv. 2024
Other Comments Or Suggestions: The proposed method is a general method, but the current work focuses on verifying it in combination with LoRA on LLama. If possible, more experiments are better.
Questions For Authors: 1) Please see weaknesses.
2) The cost of training or inference is unclear, such as GPU memory usage, training/inference time, and flops.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the reviewer’s insightful feedback. In response to their concern, we’ve expanded our analysis to include additional comparisons with three LoRA adapters: VeRA [1], DoRA [2], and MoR [3], as suggested by the reviewer. These experiments were carried out on the image classification task using the FGVC datasets. For MoR, we specifically report results with 8 experts. The detailed results are presented below:
| Method | CUB-200-2011 | NABirds | Oxford Flowers | Stanford Dogs | Stanford Cars | AVG | PPT |
| -------- | -------- | -------- | -------- | -------- | -------- | -------- | -------- |
| LoRA | 84.6 | 78.2 |98.9 | 85.1 | 77.1 |84.8 |0.82 |
| DoRA | 87.3 | 80.0 |99.1 | 87.6 | 81.9 |87.2 |0.88 |
| VeRA | 85.1 | 79.2 |97.4 | 87.3 | 76.3 |85.1 |0.88 |
| MoR | 87.6 | 82.5 | 99.3 | 89.7 | 84.7 | 88.8 | 0.89 |
| RepLoRA | **89.1** | **86.1** | **99.3** | **91.2** | **87.6** | **90.7** |**0.90** |
Following the reviewer’s suggestion, we will incorporate these results into the final revision.
When it comes to training, RepLoRA introduces only a minimal increase in parameters compared to LoRA, as seen in the number of parameters and PPT. As a result, RepLoRA does not introduce any significant additional training time, FLOPs, or memory usage when compared to LoRA. Additionally, as highlighted in the main text, the reparameterization matrices can be discarded during inference, making the inference process identical to that of LoRA.
**References**
[1] VeRA: Vector-based Random Matrix Adaptation. ICLR. 2024
[2] DoRA: Weight-Decomposed Low-Rank Adaptation. ICML. 2024
[3] MoR: Mixture of Ranks for Low-Rank Adaptation Tuning. Arxiv. 2024
---
Rebuttal Comment 1.1:
Comment: Most of my doubts have been cleared. Can reparameterization be used in other LoRA works to alleviate their suboptimal rate for low-rank matrix estimation?
Finally, I cannot offer any further advice on the mathematical derivation and analysis, so I keep my score.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer zZoN,
We would like to thank you for your response and for maintaining the positive rating of 3, which we really appreciate.
**Regarding the reparametrization for LoRA variants:** We have shown in this work that the convergence rates of low-rank matrix estimations in the original LoRA method [1] are suboptimal. Therefore, we propose the reparametrization strategy for LoRA based on its connection to Mixture-of-Experts (MoE) for improving the low-rank matrix estimation rates. On the other hand, there have not been any work analyzing that the convergence behavior of low-rank matrix estimations in other LoRA variants, namely VeRA [2] and DoRA [3], are suboptimal. However, if these rates were still suboptimal and VeRA or DoRA can be also linked to MoE in a similar fashion to the case of LoRA, then we believe that the reparametrization method would help alleviate the supoptimal rate for estimating low-rank matrices in VeRA and DoRA. Since this direction stays beyond the scope of our work, we leave it for future development.
**References**
[1] LoRA: Low-Rank Adaptation of Large Language Models. ICLR, 2022
[2] VeRA: Vector-based Random Matrix Adaptation. ICLR, 2024
[3] DoRA: Weight-Decomposed Low-Rank Adaptation. ICML, 2024 | null | null | null | null | null | null |
SECOND: Mitigating Perceptual Hallucination in Vision-Language Models via Selective and Contrastive Decoding | Accept (poster) | Summary: The paper addresses the problem of visual hallucinations in LVLMs by introducing a training-free framework called SECOND, which adaptively selects visual patches on multiple scales and applies Contrastive Decoding (CD) between the intermediate stage logits and the logits from the fine-grained expert. The paper provides theoretical motivation for the method and an empirical analysis on the hallucinations using the established benchmarks.
Claims And Evidence: The authors propose the SECOND method, which is a training-free framework to be integrated to VLMs to dynamically select more precise visual information from multi-scale patches to reduce the object hallucinations in VLMs. The authors provide an initial analysis on hallucinations which motivates the method, and evaluate SECOND on meaningful benchmarks. However, the authors could better show that SECOND is able to correctly select either broad or fine-grained visual information depending on the task.
Methods And Evaluation Criteria: While the chosen benchmarks do make sense, the proposed SECOND method is compared to only one baseline method but none of the following:
- Paying more attention to image: A training-free method for alleviating hallucination in lvlms, ECCV 2024
- Contrastive Region Guidance: Improving Grounding in Vision-Language Models without Training, ECCV 2024.
- OPERA: Alleviating Hallucination in Multi-Modal Large Language Models via Over-Trust Penalty and Retrospection-Allocation, CVPR 2024
Theoretical Claims: In my view, the current version of the paper doesn't sufficiently explain the details of the proposed method:
- it is unclear to me how attention is translated or mapped across different resolutions,
- it is not clear how transitions between the stages are performed. In my understanding, at the end of the first stage we end up with a subset of the selected patches. In the second stage, we start with an image of higher resolution but I do not understand how the patches from the first stage are used here? Is the image always sliced to the same number of patches at each stage?
Experimental Designs Or Analyses: - How were \alpha, \beta, \gamma, and \lambda determined in the experiments? Table 6 and 7 show that these parameters are not robust to changes in the data and models. If I want to use your method, how do I know how to set these hyperparameters?
- While experiments do show benefits of SECOND across different setups, there are still some cases where performance gains are marginal or even negative which makes me doubtful about its usefulness in practice. For example, in Table 1, baseline outperforms both VCD and SECOND on MSCOCO in row 3. Similar results are seen for Mistral-7B in Table 2. There is no discussion in the paper about this, despite the fact that computational cost is significantly increased. Is this a consequence of poor hyperparameter choice, specifics of the model or the benchmark? Please elaborate on these results.
- Related to above, how does computational complexity of SECOND compare to that of VCD?
Supplementary Material: I briefly went through the supplementary material.
Relation To Broader Scientific Literature: Reducing object hallucinations in VLMs is an important topic and the paper introduces a novel approach combining CD and multiscale patch selection. This differentiates it from other proposed works which are typically proposing to contrast the output distributions of multimodal inputs with those of text-only inputs.
Essential References Not Discussed: As discussed above, the following relevant works are not mentioned nor compared to:
- Paying more attention to image: A training-free method for alleviating hallucination in lvlms, ECCV 2024
- Contrastive Region Guidance: Improving Grounding in Vision-Language Models without Training, ECCV 2024.
- OPERA: Alleviating Hallucination in Multi-Modal Large Language Models via Over-Trust Penalty and Retrospection-Allocation, CVPR 2024
Other Strengths And Weaknesses: See other comments
Other Comments Or Suggestions: - Presentation of the method could be improved with more details about the method.
- nit: L not defined in def 3.1
Questions For Authors: See the comments above
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer i6dn,
We greatly appreciate your valuable feedback on our paper. We address the raised concerns and questions below.
**W1: Essential References Not Discussed**
Thank you for the suggestion. We have added the mentioned works to Sec. 2. In particular, we included OPERA in our computational cost comparison (see KN5t W2).
**W2: It is unclear how attention is translated or mapped across different resolutions.**
As described in Sec. 4.1, we extract attention maps at multiple resolutions using different patch sizes. These are resized to a common resolution and summed to form a unified attention map that captures multi-scale cues.
**W3: It is not clear how transitions between the stages are performed.**
We appreciate the feedback and would like to clarify. In SECOND, patch selection is not applied at the initial stage. The model first performs inference using tokens covering the full image, generating an attention map. Based on its attention entropy, the patch selection ratio for the next stage is determined.
In the second stage, high-resolution patches from selected regions are added for inference. This aligns with multi-scale strategies like LLaVA-OneVision, where features at different resolutions are combined. The updated attention map reflects both the initial full-image attention and the influence of newly added high-res patches.
Stage transitions are dynamic—SECOND may add patches in regions that gain attention over time. As shown in Fig. 4 (second row), a region with low initial attention becomes more prominent in later stages, demonstrating the adaptiveness of our selection process. (See also Reviewer Ekip W6.)
**W4: How were hyperparameters determined in the experiments?**
Thank you for raising this important question.
Regarding $\lambda$, while each setting has its optimal value Tab. 6, we found that $\lambda = 1.0$ consistently performs well across most conditions. This supports our recommendation of $\lambda = 1.0$ as a robust default, further backed by the trend in Fig. 6(a), where performance peaks around this value.
As for $\alpha$, $\beta$, and $\gamma$, we acknowledge the difficulty of manual tuning. Inspired by recent works [1], which explore adaptive parameter selection, we applied divergence based adaptive parameter selection. This dynamic adjustment allowed SECOND to perform close to manually-tuned baselines, achieving reasonable results on the benchmark POPE.
We believe this reduces hyperparameter sensitivity and improves the practicality of SECOND, and we plan to further develop this adaptive approach in future work.
\\(\Delta logit_{s} = α * (logit_{s} - logit_{s-1}),\\)
where \\(α = 1 - D_{bd}(S||S-1),\\)
and $D_{bd}(S||S-1)$ denotes the bounded divergence of token distribution between stage $s$ and $s-1$. (from [1])
| | POPE |
| --- | :---: |
| LLaVA-NeXT Vicuna 7B | 86.5 |
| LLaVA-NeXT Vicuna 7B + SECOND w/ $D_{bd}$ CD | 88.2 |
| LLaVA-NeXT Vicuna 7B + SECOND w/ Hard CD | **89.2** |
[1] "Code: Contrasting self-generated description to combat hallucination in large multi-modal models." NeurIPS 2024
**W5: While experiments do show benefits of SECOND across different setups, there are still some cases where performance gains are marginal or even negative.**
Thank you for pointing out this important issue. While SECOND does not yield improvements uniformly across all models and benchmarks, it is important to highlight that its primary goal is to mitigate object hallucination in VLMs. In this regard, it shows strong effectiveness—outperforming baselines in 11 out of 12 settings on the POPE benchmark (as shown in Tab. 1), which directly targets perceptual hallucination.
It also consistently improves performance on object-centric tasks such as VQAv2 across all tested models, highlighting its benefit for fine-grained object understanding. Minor drops observed in general-purpose benchmarks (e.g., MMStar, MMBench) may result from untrained patch selection slightly disrupting attention patterns—an area we plan to explore further.
Despite a few exceptions, the overall trend shows that SECOND offers reliable gains on object-level tasks. We have revised the manuscript to clarify both the strengths and limitations of our approach.
**W6: How does computational complexity of SECOND compare to that of VCD?**
Please refer to our response to Reviewer KN5t W2, where we provide a detailed comparison of per-token generation time across these methods.
**W7: Presentation of the method could be improved with more details about the method**
With responses to W2 and W3, we have revised and extended the explanations in Sec. 3 and Sec. 4 to improve the clarity and readability of our method.
**W8: nit: L not defined in def 3.1**
Thank you for pointing this out. In Def. 3.1, L refers to the length of the generated sequence. We have clarified this in the revised manuscript to avoid confusion.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the thorough reply, I raised my score accordingly. | Summary: This paper focuses on how to improve the hallucination of MLLMs. Firstly, the paper conducts some analysis of hallucinations in MLLMs, proposing two metrics, namely the Hallucination Probability and the Attention Dice Coefficient, and introducing the research motivation of needing to enhance the model's visual perception of objects. Subsequently, this paper presents a training-free method to alleviate the issues of MLLMs, named SECOND (Selective and Contrastive Decoding). This method first utilizes the model's self-attention to perform inference serially on multi-scale images, screening out the patches of the main objects of interest for the next stage of inference. Then, it fuses the inference logits of multiple stages and decodes them through contrastive decoding to obtain the final result. Finally, comparative experiments are carried out on the proposed method modules using three models, namely LLaVA-Next, LLaVA-OneVision, and Yi-VL. Additionally, ablation experiments are conducted on hyperparameters in multiple models to demonstrate the effectiveness of SECOND.
Claims And Evidence: yes
Methods And Evaluation Criteria: yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: I think this work is tradition topic with a somewhat novel method.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. This paper provides a certain degree of analysis on the hallucination of MLLM, which may inspire some new research ideas.
2. The method proposed in this paper is training-free, capable of conducting experiments on pre-trained models, and has low resource consumption.
Weaknesses：
1. It is very unreasonable in the theoretical analysis section of the paper: firstly, the formula definition of Hallucination probability proposed in Section 3 seems to lack support from relevant theoretical papers (not mentioned in the paper); Next, only use Fig 2 (a) It cannot be proven that 'Non aggregated responses preferentially exhibit lower hallucination probabilities'. Fig. 2 (a) shows two edge distributions, which can only prove that if it is known to be a Non exhaustive response, it has a higher probability of being a lower hallucination probability. Because when it is hallucinated responses, the values of these hallucination probabilities are nearly uniformly distributed.
2. Due to the hallucination of MLLM not only existing in object-centric questions or tasks, but also in more general tasks, the experimental part lacks validation of more powerful models and common benchmarks, otherwise it is difficult to prove the generality of its method. Even if it cannot be validated, the author needs to explain the specific reasons: a) the model part includes more advanced qwen2-vl and intervl2 b) the benchmark part includes MMUL/MMMU pro/MegaBenchmark, etc
Other Comments Or Suggestions: 1. The details of the method section are unclear：a) How is the visual attention used to filter patches calculated in the method, and to whom is the attention calculated? b) Is the visual path input in the current stage all from the previous stage or only from the current stage
Questions For Authors: 1. The problem of cumulative error in SECOND visual attention: SECOND uses multi-stage visual attention for patch selection, where the attention calculated in the current stage is used for the next stage of patch selection.This method seems unable to correct the already erroneous visual attention and introduces cumulative errors. For example, in the first stage, there is an error in the attention, that is, when the attention is completely focused on visual areas unrelated to the prompt, then the input patch in the next stage will have errors and cannot be corrected. So, how to improve this problem?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer Ekip,
We really appreciate your thorough review of our paper. We address the raised concerns and questions below.
**W1: The formula definition of Hallucination probability proposed in Sec. 3 seems to lack support from relevant theoretical papers (not mentioned in the paper)**
We sincerely appreciate your feedback. The definition of Hallucination Probability in Sec. 3 builds on prior works [1, 2], where the probability of a valid sequence is defined as the product of token-level probabilities:
\\(p(y|x,c) = \prod^T_{t=1} p(y_t|y_{<t}, x, c), \quad \text{where } y_{<t} \triangleq [y_0, ..., y_{t−1}]. \\)
We define Hallucination Probability as its complement, $1 - p(y|x,c)$, representing the likelihood of generating a hallucinated response. We have revised the manuscript to include these references and clarify the motivation.
[1] "Multi-modal hallucination control by visual information grounding.", CVPR. 2024.
[2] "Looking for a needle in a haystack: A comprehensive study of hallucinations in neural machine translation." ACL. 2023.
**W2: Only use Fig. 2 (a) It cannot be proven that 'Non aggregated responses preferentially exhibit lower hallucination probabilities'.**
Thank you for raising this important point. As you noted, Fig. 2(a) shows that $P_{\text{Hal}}$ is typically lower for non-hallucinated responses, while hallucinated ones exhibit a more uniform distribution. We agree that this does not imply hallucinated responses always have higher $P_{\text{Hal}}$.
However, the converse holds empirically: responses with higher $P_{\text{Hal}}$ are more likely to be hallucinated. For instance, in the [0.4, 0.5) range, the valid-to-hallucinated ratio is approximately 1:9, indicating a strong correlation. Additionally, Fig. 2(b) shows that higher $P_{\text{Hal}}$ aligns with lower Attention Dice scores, suggesting weaker visual grounding.
Our aim was to show that such high-risk responses can be mitigated by SECOND, which both reduces $P_{\text{Hal}}$ and improves grounding. We will revise the manuscript to clarify this interpretation and better explain the rationale.
**W3: a) the model part includes more advanced qwen2-vl and intervl2 b) the benchmark part includes MMUL/MMMU pro/MegaBenchmark, etc**
Thank you for your insightful comment. Due to the limited time during the rebuttal period, implementing SECOND on newly released models posed some challenges. Nevertheless, we have conducted additional experiments to compare SECOND with a broader range of more advanced models.
| | POPE (pop, f1) |
| --- | :---: |
| Qwen2-VL 7B | 87.9 |
| InternVL2 4B | 87.3 |
| InternVL2 8B | 86.7 |
| InternVL2 26B | 87.8 |
| Ivy VL 3B | 87.5 |
| Ovis 8B | 88.6 |
| LLaVA-NeXT Vicuna 7B + SECOND | **89.2** |
| LLaVA-NeXT Mistral 7B + SECOND | **88.8** |
As shown above, SECOND outperforms advanced models on the object hallucination task.
Regarding the benchmarks you mentioned, we would like to clarify that MMLU is primarily designed to evaluate LLM capabilities. For MegaBench, the length of the prompts is extremely large, and in some cases exceeds the max_token_length of models such as LLaVA-NeXT Vicuna. Therefore, we conducted additional experiments on MMMU-Pro instead. We kindly refer you to Reviewer KN5t W1 for further details.
**W4: How is the visual attention used to filter patches calculated in the method, and to whom is the attention calculated**
Thank you. We revised the manuscript for clarity. For full details, please see our response to Reviewer Lfoe W3.
**W5: Are patches from previous stages reused?**
Yes, visual patches are accumulated across stages. Each stage uses both newly selected and retained patches to refine grounding. While this was indicated in Fig. 1, Fig. 3 and Sec. 4.1, we have now clarified it further.
**W6: seems unable to correct the already erroneous visual attention and introduces cumulative errors.**
Thank you for this insightful observation. We clarify that patch selection in SECOND is not restricted to a fixed or narrowing set of regions. As described in Sec. 4.1, the selection ratio ($P_{\text{select}}$) is dynamically adjusted across stages based on changes in attention entropy. When entropy increases—signaling higher uncertainty—the selection ratio can also increase, allowing inclusion of previously unselected but relevant patches.
Our Contrastive Decoding further ensures that newly added patches, even if missed earlier, can still influence the final output—helping correct early-stage attention errors. As shown in Fig. 4, some patches initially receive high attention but decrease as new patches are added. Also in the second row of Fig. 4, we observe the model gradually shifting its focus toward the top-right region, which initially had low attention.
To address cases of completely misaligned attention, we compare SECOND with a variant using all patches (no selection) in Tab. 4. SECOND outperforms this baseline, showing its robustness against cumulative attention errors. | Summary: In this paper, a decoding method for LVLMs named SECOND is proposed. SECOND consists of selective multi-scale feature integration and multi-stage contrastive decoding. The first method, selective multi-scale feature integration leverages multi-scale feature map with patch selection scheme, where important patches are progressively selected in high-resolution features based on lower resolution attention values. Multi-stage contrastive decoding contrasts outputs obtained with multi-scale features, thereby prioritizing outputs of relative ‘experts’ with better feature maps.
Claims And Evidence: The authors’ claims are supported with proper observations and analyses.
Methods And Evaluation Criteria: The proposed methods are sound. Also, experiments on POPE benchmark and various multimodal benchmarks supports the method.
Theoretical Claims: The authors make some theoretical claims that are supported with observations and proofs.
Experimental Designs Or Analyses: Proper ablation studies are provided, which validates the effectiveness of each method.
Supplementary Material: I have read through every section of the supplementary material, where further analysis, experiments, proofs, and implementation details are provided.
Relation To Broader Scientific Literature: This work provides a simple yet effective method to enhance LVLMs by effectively utilizing multi-scale features. Also, the observations provided in the paper help understanding problems of LVLMs.
Essential References Not Discussed: Since there are multiple works [1-6] utilizing contrastive decoding to mitigate hallucination problem of LVLMs, discussion with those works should be provided.
[1] Huo et al., Self-Introspective Decoding: Alleviating Hallucinations for Large Vision-Language Models, ICLR 2025
[2] Zhuang et al., VASparse: Towards Efficient Visual Hallucination Mitigation for Large Vision-Language Model via Visual-Aware Sparsification, CVPR 2025
[3] Cho et al., Do You Keep an Eye on What I Ask? Mitigating Multimodal Hallucination via Attention-Guided Ensemble Decoding, ICLR 2025
[4] Kim et al., VACoDe: Visual Augmented Contrastive Decoding, ICML Workshop 2024
[5] Park et al., ConVis: Contrastive Decoding with Hallucination Visualization for Mitigating Hallucinations in Multimodal Large Language Models, arXiv 2024
[6] Lee et al., Delve into Visual Contrastive Decoding for Hallucination Mitigation of Large Vision-Language Models, arXiv 2024
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: Although the paper is generally well-written, there are some areas that could be improved:
1. L153 (left column): The implication of the attention Dice coefficient could be briefly introduced for better clarity. For example, consider adding a sentence like: *“A higher attention Dice coefficient indicates that an LVLM properly focuses on objects.”*
2. L163 (left column): The paper states that *“hallucinated responses tend to have higher Attention Dice scores.”* However, in Figure 2-(b), hallucinated responses appear to have **lower** scores compared to non-hallucinated responses. Is this a mistake in the paper, or have I misunderstood?
3. L255 (left column): The explanation of how visual attention is generated and interpreted is not detailed enough. Additionally, the selection process is overly simplified. While Section D of the supplementary material provides further details, it would be better to introduce more information in the main paper and explicitly reference the exact section of the supplementary material.
Questions For Authors: Please kindly address concerns in other sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer Lfoe,
We greatly appreciate your valuable feedback on our paper. We address the raised concerns and questions below.
**W1: L153 (left column): The implication of the attention Dice coefficient could be briefly introduced for better clarity.**
Thank you for the insightful comment. To improve clarity, we have revised main manuscript by adding a brief explanatory sentence, “A higher Attention Dice coefficient indicates that an LVLM properly focuses on objects”. This addition will help readers better understand the meaning and importance of the Attention Dice Coefficient in our theorem.
**W2: The paper states that “hallucinated responses tend to have higher Attention Dice scores.” However, in Fig. 2 (b), hallucinated responses appear to have lower scores compared to non-hallucinated responses. Is this a mistake in the paper, or have I misunderstood?**
Thank you for pointing this out. You are correct — there is a mistake in the original text. Hallucinated responses actually tend to have lower Attention Dice Coefficient, as correctly shown in Fig. 2 (b). We have corrected the sentence to reflect this and apologize for the confusion.
**W3: L255 (left column): The explanation of how visual attention is generated and interpreted is not detailed enough. Additionally, the selection process is overly simplified. While Section D of the supplementary material provides further details, it would be better to introduce more information in the main paper and explicitly reference the exact section of the supplementary material.**
We are grateful for your constructive suggestion. To clarify, we describe the computation of attention in Section 3.2 (for calculating the Attention Dice Coefficient), and we adopt the same formulation in our methodology (Sec. 4).
The visual attention used to filter patches is derived from two sources:
1. Self-attention maps from the vision encoder of the LVLM, which operate over 2D spatial image patches.
2. Cross-attention maps from the LLM decoder, which capture the attention from generated textual tokens to the visual tokens (i.e., image patches).
To compute a unified attention signal that reflects both visual and textual modalities, we multiply these two attention maps element-wise. Since the cross-attention is defined over flattened visual tokens (i.e., in a 1D format), we first map the 1D token-based attention values back to their corresponding 2D spatial coordinates to align with the vision encoder’s attention layout. This alignment enables meaningful element-wise fusion of the two attention maps.
This fused attention allows us to effectively estimate the contribution of each image patch to the generated tokens, which we then use to guide patch filtering in our method. We will revise the manuscript to make this computation process more explicit and improve overall clarity.
**W4: Essential References Not Discussed**
We sincerely thank the reviewer for highlighting this important references. We fully agree that recent decoding-based approaches—such as VASparse, VACoDe, ConVis, SID, and Ensemble Decoding (ED)—have made important contributions to hallucination mitigation in vision-language models (VLMs). To provide a more comprehensive and contextualized discussion, we have incorporated these references into the Sec. 2. Related Works of the revised manuscript. Furthermore, we have added explicit comparisons between each of these methods and our proposed SECOND approach in the main text, highlighting key distinctions in terms of decoding strategy, use of contrastive signals, reliance on external augmentations, and computational characteristics. We hope this addition strengthens the clarity of our contributions and the positioning of our work within the existing literature.
---
Rebuttal Comment 1.1:
Comment: I have carefully read the authors' rebuttal as well as their responses to other reviewers.
Overall, I find the paper valuable, and my concerns regarding its clarity have been adequately addressed.
Therefore, I maintain my original rating. | Summary: This paper introduces SECOND, a training-free approach to mitigate perceptual hallucination in LVLM. More specifically, it progressively refines (by patch selection) multi-scale visual information in an object-centric manner, and uses multi-stage contrastive decoding to reduce perceptual hallucinations. Results show it outperforms baselines across diverse benchmarks.
## update after rebuttal
The rebuttal has clarified my concerns. I am happy to maintain my original recommendation.
Claims And Evidence: The experiments, evaluations, analysis and theory proof support its claim.
Methods And Evaluation Criteria: The methods involve two core components: 1) adaptive multi-scale patch selection, 2) multi-stage contrastive decoding. Ablations show both are important in mitigating perceptual hallucinations.
The authors use the POPE benchmark to evaluate perceptual hallucination, and use VQAv2, MMStar, and MMBench for general tasks. However, more tasks could be introduced to verify SECOND’s effectiveness on common VLM tasks, such as captioning, document understanding, infographics reasoning etc.
Theoretical Claims: The authors raise the hypothesis that a model’s ability to focus accurately on target objects significantly reduces hallucination risk, which was proved via Attention Dice Coefficient experiments. Then it proves that multi-stage patch selection increases the Attention Dice Coefficient, thereby reducing the probability of hallucination.
Experimental Designs Or Analyses: The authors implement SECOND on three recent LVLMs: LLaVA-NeXT, LLaVA-OneVision, and Yi-VL; evaluate these models on the POPE benchmark for perceptual hallucination and VQAv2, MMStar, and MMBench for general tasks. Qualitative results are also presented to give readers insight.
Supplementary Material: The supplementary material is duplicate with the appendix in this paper.
Relation To Broader Scientific Literature: This paper successfully extends the concept of Contrastive Decoding from LLMs to LVLMs, which might be insightful for the community.
The theories and proofs presented in this paper also provide valuable insights for the community.
Essential References Not Discussed: no
Other Strengths And Weaknesses: Strengths
- The ideal is novel and further strengthened by the theory proof.
- The paper is well written and easy to read.
- Theories are presented clearly.
Weaknesses
- It’s unclear how efficient the method is, with additional multi-stage computation.
- As mentioned above, more common VLM tasks can be added to verify the effectiveness of the methods, such as in document instead of semantic understanding.
Other Comments Or Suggestions: no
Questions For Authors: no
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer KN5t,
Thanks for your valuable feedback! We provide point-by-point responses to address your concerns below.
**W1: More tasks could be introduced to verify SECOND’s effectiveness on common VLM tasks, such as captioning, document understanding, infographics reasoning etc.**
Thank you for this valuable suggestion. To further substantiate the effectiveness of SECOND on a broader range of common VLM tasks, we have conducted additional experiments on MMMU_Pro, complementing the previously reported results on MMStar and MMBench.
These benchmarks collectively provide a comprehensive evaluation across a diverse set of task categories, including instance relation reasoning, diagram reasoning, calculation, and scene understanding—covering many of the task types you mentioned. The new result of MMMU Pro, presented below, offer additional evidence supporting the robustness and generalizability of SECOND across diverse VLM challenges.
This additional experiment has been added to Appendix of the main manuscript. We hope this additional evaluation addresses your concern.
| | CD | MMMU_Pro |
| --- | :---: | :---: |
| LLaVA-NeXT Vicuna 7B | X | 16.1 |
| LLaVA-NeXT Vicuna 7B + SECOND | X | 16.7 |
| LLaVA-NeXT Vicuna 7B + SECOND | O | 16.9 |
| LLaVA-OneVision Qwen 0.5B | X | 14.5 |
| LLaVA-OneVision Qwen 0.5B + SECOND | X | 15.0 |
| LLaVA-OneVision Qwen 0.5B + SECOND | O | 15.0 |
**W2: It’s unclear how efficient the method is, with additional multi-stage computation**
Thank you for highlighting this important point. To address concerns regarding the computational efficiency of SECOND, we have measured and compared the per-token generation time of our method against the baseline VCD and the method OPERA[1] (a widely used approach for mitigating VLM hallucination, proposed by Reviewer i6dn).
The results are summarized as follows:
| | VCD | SECOND(3-stages) | SECOND(4-stages) | OPERA |
| --- | :---: | :---: | :---: | :---: |
| LLaVA-NeXT Vicuna 7B (sec / token) | 0.41 | 1.28 | 1.80 | 5.00 |
| Yi-VL 6B (sec / token) | 0.26 | 0.73 | - | 4.79 |
These measurements demonstrate that while SECOND introduces a modest increase in computation due to its multi-stage patch selection, the increase remains manageable. Importantly, this additional computational cost is well-justified by the consistent performance improvements on hallucination mitigation and general VLM performance across our experiments. We will include these results in the revised manuscript to provide a clearer picture of SECOND’s efficiency.
[1] "Opera: Alleviating hallucination in multi-modal large language models via over-trust penalty and retrospection-allocation." CVPR. 2024. | null | null | null | null | null | null |
Time Series Representations with Hard-Coded Invariances | Accept (poster) | Summary: This paper posits that invariances to the deformations are critical for time series tasks such as classification. The paper mathematically formulates the invariance in the language of group theory and further technically designs efficient and hard-coded invariant convolutions for specific deformations commonly observed in time series (scaling, offset shift, and trend). Experiments are conducted on time series classification and anomaly detection tasks to verify its effectiveness.
Claims And Evidence: The claims are supported by both theoretical and empirical evidence.
Methods And Evaluation Criteria: The mathematical formulation of the problem and the design of the method are clear, and the selection of evaluation criteria is well-justified.
Theoretical Claims: The mathematical formulation is rigorous and sound, building on group theory and projection operators. Specifically, propositions 1–2 are correctly proven using orthogonal projection operators, ensuring invariance to specified deformations.
Experimental Designs Or Analyses: The experiments are thorough, including the results of multiple tasks (classification, anomaly detection) and efficiency analysis.
However, some of the results raised my concerns:
1. In Table 1, InvConvNet is not optimal on normalized data (without additional deformation), which questions its practicality.
2. In Table 2 and Table 11, the performance improvement is not markedly significant. For instance, InvConvNet compared to the second-best baselines:
UEA 71.81 over 71.29, +0.52 (0.7%),
UCIHAR 96.63 over 96.04, +0.59 (0.6%),
Epilepsy 98.43 over 98.38, +0.05 (0.05%).
Supplementary Material: The supplementary material, including proofs, experimental details, additional results, and visualizations, is well-organized and improves the quality of the paper.
Relation To Broader Scientific Literature: This work connects to broader literature by formalizing time series invariances through group actions, extending principles from image invariance to the time series domain. It draws inspiration from the traditional time series mining methods' focus on invariance (e.g., warping invariance through DTW, amplitude and offset invariances through Z-normalization) and proposes invariant convolutions for deep learning, offering a new perspective for handling deformations in time series analysis.
Essential References Not Discussed: To the best of my knowledge, all key references have been thoroughly addressed in the paper.
Other Strengths And Weaknesses: Strengths:
1. The paper introduces a novel approach to capturing invariances from deformations in time series, which is significant for tasks such as time series classification. Technically, a novel convolution, Inv. Conv, is proposed to keep invariant to rigid deformations. It is computationally efficient through FFT.
2. As mentioned in Theoretical Claim, the mathematical formulation is rigorous and sound, building on group theory and projection operators.
3. The experiments are thorough, including the results of multiple tasks (classification, anomaly detection) and efficiency analysis. Additional results in supplementary material further improve the quality of the paper.
Weaknesses:
1. The presentation of the paper could be improved; some sections are dense, making it challenging to follow for those less familiar with group theory.
2. As mentioned in Experimental Design, in Table 1, InvConvNet is not optimal on normalized data (without additional deformation), which questions its practicality.
3. As mentioned in Experimental Design, the performance improvement is not markedly significant in Table 2 and Table 11.
Other Comments Or Suggestions: I suggest relocating Figure 2 to an earlier section of the manuscript, facilitating an intuitive comprehension of deformation for readers as they engage with the introduction section.
Questions For Authors: 1. Based on Weakness 1, InvConvNet does not exhibit optimal performance on normalized data, and it only demonstrates a performance advantage when artificial deformations are introduced. However, raw data inherently possesses distribution shifts. Thus, what is the practical significance of artificially adding deformations? Furthermore, how can you ensure that the added deformations are justifiable for the specific dataset? For instance, introducing certain deformations to ECG signals might cause anomalies to the entire dataset that contravene established medical principles.
2. Time series forecasting methods are discussed in Related Work. Can invariant convolution enhance the performance of time series forecasting?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's time and thoughtful feedback. In the following, we thoroughly address each identified weakness and question.
**[Experimental Design]**
- **Performance on UCR normalized data:**
We address your concern in Q1 below. To clarify, synthetic deformations are used only in test sets for the robustness study of convolutions (Section 4.1, Table 1). In contrast, in all other experiments (Sections 4.2–4.4 for classification and Appendix A.5.1 for anomaly detection), performance is evaluated on default data without added deformations.
- **Significance of results:** We invite the reviewer to see the critical diagram difference for UEA in the rebuttal for **reviewer gvG9**.
**[Other]**
> The presentation of the paper could be improved [...].
To enhance readability, we will move Figure 2 to an earlier section of the manuscript to better standard deformations and add a brief intuitive introduction in the method section. See our response to **reviewer Bfty** in section **[Clarity]** for details.
Replies to Questions:
> Q1. *InvConvNet does not exhibit optimal performance on normalized data [...]. What is the practical significance of artificially adding deformations?*
In the robustness experiment ("I. Robustness to Deformations", section 4.1), the performance of invariant convolutions compared to normal ones on the plain (i.e., z-normalized input without deformations) is better for 2 out of 5 plain UCR datasets. It is still close for the rest of the cases (average -4.7\% drop for the 3 data cases). Contrary when synthetic deformations are added, the performance drops for normal convolutions are around -50\% (on average for the 4 considered deformations), whereas for the trend invariant convolution, this drop is just around -2\% (on average for the 4 considered deformations) showing the competitiveness and robustness of the proposed layer in comparison to its standard counterparts.
The motivation for the robustness study on UCR datasets is as follows: Most UCR datasets, including those used in this study, are already z-normalized. Their univariate nature, limited class diversity, and relative trend stability make classification easier for normal convolutions. To systematically assess the impact of synthetic deformations, we use these datasets in a controlled setting, progressively increasing deformation complexity (from offset shifts to linear trends and smooth random walks) to evaluate how different convolutional components, including those invariant to such distortions, respond.
> Q2. *How can you ensure that the added deformations are justifiable for the specific dataset?*
Offset and trend invariances are common in real-world applications like PPG monitoring and ECG analysis (see reply **[Other]** to **reviewer gvG9**). They are tackled by baseline wander removal and offset correction techniques that preserve physiological signals while eliminating low-frequency noise. The closest easy-to-generate deformation, a smooth random walk, is included in the robustness experiment (see Table 1).
> Q3. *Can invariant convolution enhance the performance of time series forecasting?*
Our invariant layers, combined with the example decoder used for anomaly detection, naturally extend to forecasting by employing the same lightweight decoder based on linear layers applied to the learned coefficients. We next provide some preliminary results (in MSE) for the ETT-small datasets (for horizon length h=96), where we use a fixed seed and compare our approach against 8 baselines (most derived from the package Time Series Library).
| Datasets (h=96) | **InvConvNet** | **TimeMixer** | **PerimidFormer** | **iTransformer** | **PatchTST** | **DLinear** | **TimeNet** | **FedFormer** | **Autoformer** |
|-----------------|----------------|---------------|-------------------|------------------|--------------|-------------|-------------|----------------|----------------|
| **ETTm1** | 0.342 | **0.319** | 0.325 | 0.345 | 0.325 | 0.347 | 0.337 | 0.365 | 0.486 |
| **ETTm2** | 0.193 | **0.178** | 0.180 | 0.184 | **0.178** | 0.195 | 0.187 | 0.194 | 0.215 |
| **ETTh1** | 0.426 | 0.388 | **0.377** | 0.402 | 0.380 | 0.407 | 0.394 | 0.378 | 0.463 |
| **ETTh2** | 0.340 | **0.289** | 0.322 | 0.299 | 0.312 | 0.357 | 0.330 | 0.349 | 0.343 |
These results, achieved without hyperparameter tuning (in less than a week), are close to SOTA performance, highlighting their potential. Future improvements include testing hybrid architectures for the decoder (e.g., transformers) to enhance finer granularity, capture longer dependencies, and unsupervised pretraining for better generalization.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. While some issues were addressed, my core concern remains unresolved: the limited performance improvement of InvConvNet challenges its practical significance. During my review, I carefully examined the results in the main text and appendices. In the anomaly detection task (Table 9), the proposed model only achieves the best performance on SWaT, and the improvement is marginal (92.82 vs. 92.71, a 0.001% increase). For the classification task (Table 11), the 1st count is fewer than ResNet and Rocket, and the accuracy gains in those cases are similarly modest. Although InvConv demonstrates robustness to certain deformation in Table 1, it presents suboptimal performance on normalized data. In my view, robustness evaluations based on synthetic deformation are meaningful only if the model performs well on real-world datasets. Therefore, I maintain my original rating.
---
Reply to Comment 1.1.1:
Comment: We sincerely thank the reviewer for their feedback on our work. We next address the concerns raised regarding the performance improvements of the example architecture InvConvNet.
First, we would like to draw the reviewer’s attention to the fact that, rather than proposing a general-purpose architecture, our main goal was to **introduce versatile layers** that integrate easily into simple models and extract deformation-invariant representations **for improved robustness**, which is supported both theoretically and empirically. To illustrate this, we used simple lightweight architectures that consistently match or surpass more complex baselines across experiments.
The selected UCR datasets are z-normalized, trend-stable (as shown in Fig. 7 for FordB), and large in size, making raw data classification relatively easy, resulting in similar performances between standard and invariant convolutions. However, **under artificial deformations, standard convolutions performances drop sharply** (−48\% to −59\%), **while invariant convolutions remain robust** (0\% to −6\%). **Transfer learning results in Section 4.2 further support our robustness claims**, showing **around 4\% gains** over contrastive methods and standard convolutions.
For the classification and anomaly detection experiments on raw data, we next present mean rank comparisons for a fairer assessment across datasets, as they emphasize relative performance over absolute scores. This approach offers a balanced robustness evaluation and allows statistical significance analysis.
### Table: Mean Rank in Classification Accuracy (\%) for all considered datasets (UEA + 3 additional datasets) in section 4.2
| Datasets | InvConvNet | TimesNet | PatchTST | Crossformer | TSLANet | DLinear | Inception | ResNet | Cnn | Rocket |
|------------------------------------------|------------|----------|----------|--------------|---------|---------|-----------|--------|--------|----------|
| *UEA + UCIHAR, Sleep-EDF, Epilepsy* | **3.00** | 5.6964 | 6.5714 | 6.0357 | 4.8036 | 7.7143 | 6.7500 | 4.8571 | 5.7857 | **3.7857** |
| **CD Value** | 1.80 | | | | | | | | | |
We evaluated 10 models on multivariate classification benchmarks (UEA, UCIHAR, Sleep-EDF, Epilepsy) using mean ranks based on Accuracy and assessed significance with the Friedman test (CD = 1.80, α = 0.1, Test Statistic = 55.78, p = 0.0000). The null hypothesis is rejected, confirming statistical performance differences. Our **InvConvNet achieves the best mean rank (3.00), followed by Rocket (3.79)**, with both forming the top-performing group in the Nemenyi post-hoc test.
### Table: Mean Rank in F1-score (\%) on $5$ Anomaly Detection (AD) Datasets
| Datasets | InvConvNet | TimesNet | PatchTST | TSLANet | ETSformer | FEDformer | LightTS | DLinear | Autoformer | Pyraformer | Informer | Reformer |
|-----------------------|------------|----------|----------|---------|-----------|-----------|---------|---------|-------------|-------------|----------|----------|
| AD Benchmark (#5) | *4.6* | **3.6** | 6.0 | 5.0 | 8.0 | 8.5 | 6.4 | 5.6 | 7.3 | 7.8 | 7.6 | 7.6 |
| CD Value | 7.56 | | | | | | | | | | | |
We evaluated 12 models on 5 anomaly detection datasets using mean ranks based on F1-score and the Friedman test (statistic = 10.14, p = 0.5180, CD = 7.56 at $\alpha = 0.1$). Based on the p-value, no statistically significant differences were found, and all models belong to the same group. **InvConvNet ranks second (4.6), closely behind TimesNet (3.6)**, indicating competitive and robust performance against several baselines.
In terms of runtime comparisons, **InvConvNet is 6.6× faster than TimesNet** and **5.3× faster than TSLANet in time per epoch** on average for the $5$ datasets. For instance, On SMD, it's 22.5× faster than TimesNet and 11.4× faster than TSLANet, with only minor performance drops (-0.56\% and -0.28\%). These time cost results align with Figure 3, where InvConvNet is 1.2× faster than TSLANet on Heartbeat (from UEA) while improving classification accuracy by 1.6\% (77.40\% vs. 75.77\%).
We hope the above clarifications highlight the robustness, consistent performance, and computational efficiency of the example InvConvNet architectures, which primarily serve to evaluate our theoretically grounded invariant convolutions. We greatly appreciate your continued interest in our work and hope that our justifications further highlight the potential and impact of our proposed convolutional layers for different time series applications. | Summary: This paper proposes a novel mathematical method to consider the deformation-invariance during representation learning, which is beneficial for downstream tasks such like classification. It designs a G-variant convolution model called TS-TCC to obtain deformation-invariant embeddings, which provides robustness by decoupling the key information from deformations. Theoretically, this paper proposes using group actions to represent deformations and proves that orbit-injective embedding could map the orbit (the deformations on some time series) to the same embedding, thus avoiding the adverse effects from deformations during training. Empircally, this paper constructs the Invariant & Orbit-injective embedding through a convolution and validates its performance on the classification task.
## update after rebuttal
Thank you for the respnse, which clarify things. I will keep my relatively positive perspetive.
Claims And Evidence: The paper manages to solve the deformation phenomenon in time series representation learning, which hinders the capture of key information. To achieve this, it starts from a mathematical methodology, utilizes the group theory and mesurement theory to construct a specific convolution. The theoretical aspects are correct and can support the author's motivations.
However, the basic assumptions about the deformation phenomenon seem not strong enough. The showcase in Figure 1 conveys the information that the key information (seems to be the period) could be coupled in the trend ( a kind of deformation). While in forecasting tasks, such decomposition methods (moving average, convolutions) are widely used [1,2,3] to extract the trend. CycleNet [4] has also demonstrated that global shared periods can be easily extracted through a learnable matrix. In other words, the authors seem only consider some naive linear deformations (the equation 2 and Figrue 2), are ANNs really hard to handle these?
[1] Autoformer: Decomposition transformers with auto-correlation for long-term series forecasting.
[2] Are transformers effective for time series forecasting?
[3] Duet: Dual clustering enhanced multivariate time series forecasting.
[4] Cyclenet: enhancing time series forecasting through modeling periodic patterns.
Methods And Evaluation Criteria: Though the methodology is correct and novel, the benchmarking is somewhat weak. The paper proposes a representation method while only validating its performance on classification tasks. Since the deformation phenomenon is ubiquitous, why not explore its performance on various downstream tasks such as forecasting, anomaly detection (should be discussed in the main text)?
Theoretical Claims: The proofs are correct.
Experimental Designs Or Analyses: It is recommended to evaluate the effects on several other downstream tasks such as forecasting and anomaly detection. The baselines are also somewhat outdated that only one work is published in 2024. The authors can take UP2ME [5], Peri-midFormer [6] into consideration.
[5] UP2ME: Univariate Pre-training to Multivariate Fine-tuning as a General-purpose Framework for Multivariate Time Series Analysis
[6] Peri-midFormer: Periodic Pyramid Transformer for Time Series Analysis
Supplementary Material: Some additional proof details, experimental settings have been provided in the appendix.
Relation To Broader Scientific Literature: Discussing some transformation problems from the perspective of group theory as in this paper is a research prospect, because mathematical methods often bring strong constraints. As long as the assumptions are correct, the probability of effectiveness will be greater.
Essential References Not Discussed: More recent studies should be discussed in the related works and added as baselines. See [5] - [6].
Other Strengths And Weaknesses: none
Other Comments Or Suggestions: none
Questions For Authors: see previous sections
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for their time and thoughtful evaluation of our work. In the following section, we address any concerns raised.
**[Claims and Evidence]**
> "However, the basic assumptions about the deformation phenomenon seem not strong enough[...] While in forecasting tasks, such decomposition methods (moving average, convolutions) are widely used [...]"
For time series forecasting, the suggested papers [1,2,3,4] assume a seasonal-trend decomposition of time series to derive suited ANN architectures. Most methods employ a (learnable) moving average kernel to infer the trend and propose different ways to deal with residual time series. The average moving kernel corresponds to a specific deformation in the proposed framework: the offset shift (see Figure 2). Assuming such offset-invariant kernels, the proposed layer offers different views of the residual time series. When focusing on trend deformations, the trend approximation could be better inferred by assuming a higher-order Taylor expansion (linear, quadratic, etc.). In the anomaly detection (Appendix A.5.1) and forecasting experiments (see rebuttal reply **Q3** to **reviewer MxbV**), we also leverage trend-residual decomposition in lightweight architectures by feed-forwarding the projections coefficients to the reconstruction layer.
In classification, PerimidFormer (Classification Table in rebuttal response to **reviewer Bfty**) and Dlinear (Table 2 of the manuscript) are also based on a trend-residual decomposition, yet are significantly outcompetes by the proposed invariant convolutions. For instance, on the UEA datasets, our example architecture InvConvNet, performs better than PerimidFormer and Dlinear (acc: 71.81 vs (59.71 and 61.51 resp.)), suggesting that deformation-based trend invariance is better suited than standard trend-residual decomposition for classification with neural networks. Overall, the proposed layer seems more versatile and robust compared to existing architectures on several tasks while guaranteeing state-of-the-art performances.
> "The authors seem only consider some naive linear deformations [...] are ANNs really hard to handle these?"
Standard ANNs often struggle with generalization on noisy, non-stationary time series, as illustrated in Figure 1, where a standard CNN fails to capture relevant ECG features. To test whether CNNs can learn invariance, we conduct a robustness experiment (Table 1), showing that classification performance declines as datasets are progressively deformed. Standard convolutions prove sensitive to spatiotemporal distortions (avg. acc. drop: -50\%), whereas hard-coded invariant convolutions offer better generalization (avg. acc. drop: -2\%) than contrastive learning (avg. acc. drop: -23\%). Figure 8 (Appendix) further visualizes this, revealing that standard CNN feature maps become distorted, while invariant convolutions retain structured representations (see Figure 7 for corresponding FordB dataset deformations). These findings align with (Kvinge et al., 2022) for image data. Finally, in transfer learning (Table 4), invariant convolutions surpass standard architectures and contrastive frameworks by at least 4\%.
- Kvinge, H., Emerson, T., Jorgenson, G., Vasquez, S., Doster, T., \& Lew, J. (2022). In what ways are deep neural networks invariant and how should we measure this?. NeurIPS, 35, 32816-32829.
>The paper proposes a representation method [...] tasks such as forecasting, anomaly detection?
We conduct extensive experiments across diverse real-world applications to validate our theoretical framework of time series invariant convolutions, leveraging common offset and shift invariances in shallow (Figures 5 and 6) and lightweight example architectures (Figure 3). We have demonstrated robustness against offset and trend deformations (Section 4.1), strong performance in multivariate classification (Section 4.2), and transfer learning for classification (Section 4.3). Additionally, we extend our analysis to anomaly detection in Appendix A.5.1. Rather than proposing a general-purpose architecture, targeted to specific time series tasks, our goal was to develop versatile layers that integrate seamlessly with existing methods to enhance robustness. To illustrate this, we employ lightweight architectures—such as linear decoders for regression—that, despite their simplicity, match or surpass complex baselines. While our current focus is classification and anomaly detection, our approach naturally extends and holds promise for forecasting, as noted in our response and experiments provided to **reviewer MxbV** (rebuttal reply **Q3**).
**[Experimental Designs Or Analyses]**
We show improved performance against the suggested baselines UP2ME [5] and PerimidFormer [6]. Please refer to the Tables in the rebuttal reply to **reviewer Bfty**. We will also include a discussion about the additional baselines in the revised version of the manuscript (not added here due to the word limit). | Summary: The paper proposes convolutional neural network operations explicitly designed with hard-coded invariances (e.g., scaling, offset shift, linear trends) for improved time series representation learning. By formulating invariances through group theory and embedding them directly into convolutional layers, the authors show empirically that their method enhances robustness against common temporal deformations, achieves competitive or superior accuracy across benchmark classification tasks, and offers computational efficiency advantages over learned invariances or standard CNN approaches.
## update after rebuttal
Most of my concerns have been addressed. I will keep my score to support the paper.
Claims And Evidence: The claims presented in the paper are generally supported by clear and convincing evidence. The authors provide a thorough mathematical formulation of their hard-coded invariant convolutions and validate the theoretical properties empirically on multiple tasks, including synthetic deformation robustness tests, benchmark classification datasets, and transfer learning scenarios. The experimental setup is extensive and compares against relevant state-of-the-art baselines, clearly supporting the claims regarding improved robustness and competitive accuracy. However, while the authors claim computational efficiency benefits through FFT-based convolutions, additional explicit runtime comparisons or complexity analyses against more baseline architectures (especially in larger-scale or real-world scenarios) would further strengthen this claim.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are generally appropriate. But I think authors should include some more stronger baselines ([1] [2] etc.). Also, I suggest authors to provide more visualization results to demonstrate the effectiveness of capturing invariances in time series.
[1] iTransformer: Inverted Transformers Are Effective for Time Series Forecasting
[2] TimeMixer
Theoretical Claims: I checked the correctness of the theoretical claims presented, specifically focusing on the mathematical formulations related to group invariances and the definition of invariant convolution operators (Section 3, including Propositions 1 and 2). The proofs provided in Appendix A.1 (referred to clearly within the paper) appear mathematically sound and correctly derived, relying appropriately on established concepts from group theory and functional analysis. But I am not very familiar with this field, so I am not very confident about my judgement.
Experimental Designs Or Analyses: I have checked the soundness/validity of experimental designs and analyses. The experimental designs and analyses presented in the paper appear sound and valid. Specifically, the robustness evaluation involving synthetic deformations (offset shifts, linear trends, random walks) provides clear evidence to support the claimed invariances. Benchmarking against multiple state-of-the-art baselines across diverse datasets from the widely used UCR and UEA archives ensures rigorous comparative assessment. The transfer learning experiments are also well-designed, clearly illustrating the generalization capabilities of the proposed method. One minor area for improvement could be providing additional details on hyperparameter tuning and statistical significance testing for the observed improvements to further reinforce the validity of the conclusions.
Supplementary Material: I have reviewed the supplementary material, which includes code implementation of proposed models. However, I noticed in the checkpoint folder is empty.
Relation To Broader Scientific Literature: The paper's key contributions closely relate to recent research in deep learning for time series, particularly efforts to enhance model robustness via invariant representations. Specifically, the authors build upon concepts from group theory and invariant/equivariant neural networks, aligning with prior research on hard-coded invariances in domains such as images and graphs (e.g., translation invariance in CNNs, permutation invariance in GNNs). Unlike prevalent methods that introduce invariances implicitly through data augmentation and contrastive learning (e.g., TS-TCC, TS2Vec), this paper explicitly incorporates invariances into convolutional architecture design, extending established ideas (e.g., ROCKET's random convolutions) with rigorous theoretical foundations. Thus, the presented method bridges prior theoretical findings about invariance modeling with practical CNN-based approaches widely adopted in time series classification, positioning itself clearly and convincingly within the broader scientific landscape.
Essential References Not Discussed: To my best knowledge, essential references are discussed.
Other Strengths And Weaknesses: Strengths:
* Originality: The paper demonstrates clear originality by creatively combining established mathematical concepts (group invariances) with convolutional neural network architectures, leading to explicit and computationally efficient invariant representations for time series.
* Significance: The contributions are significant, addressing important practical challenges in the robustness of deep learning models for real-world temporal data.
Weaknesses:
* Clarity: the mathematics framework is hard to understand. It would be better if authors could give some intuitive explanations.
Other Comments Or Suggestions: I am willing to raise my score if authors could address my concerns.
Questions For Authors: I do not have other questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate the reviewer's time and effort in evaluating our work. Below, we provide our responses to the main suggestions.
**[Claims And Evidence]**
> "authors claim computational efficiency benefits [...], additional explicit runtime comparisons [...]".
We have demonstrated the computational efficiency of the proposed invariant layers over baselines, with memory complexity and training time comparisons shown on the UEA Heartbeat dataset (with 61 channels and 405 timestamps) in Figure 3. Similar time comparisons on larger datasets will be included in the revised manuscript. More details on the fast computation of our convolutional layers via FFT can be found in Section 3.2 (pages 4-5).
**[Methods and Evaluation Criteria]**
- **Additional Experiments.**
We next present comparisons for classification on the 26 UEA datasets and the 5 anomaly detection (AD) datasets, evaluating the additional methods: TimeMixer, iTransformer, Peri-midFormer, and UP2ME
## Additional Results Classification Acc.(\%)
| Datasets | **InvConvNet** | TimeMixer | iTransformer | PerimidFormer | UP2ME |
|---------------------|----------------|-----------|--------------|---------------|--------|
| **UEA** (26 datasets) | **71.81 ± 0.80** | 64.60 ± 1.59 | 64.42 ± 2.05 | 59.71 ± 3.03 | 54.57 ± 3.88 |
## Additional Results Anomaly Detection
| Datasets | **InvConvNet** | TimeMixer | iTransformer | PerimidFormer | UP2ME (4/5 datasets) |
|-----------|-----------------|-----------|--------------|---------------|----------------------|
| **SMD** | **84.05 ± 0.16** | 83.20 ± 0.06 | 82.38 ± 0.99 | 83.34 ± 0.63 | **84.34 ± 0.13** |
| **MSL** | **80.68 ± 0.01** | 67.12 ± 3.33 | 72.66 ± 0.04 | 80.93 ± 0.06 | 80.66 ± 0.01 |
| **SMAP** | **68.29 ± 0.07** | 65.55 ± 0.32 | 66.86 ± 0.08 | 67.62 ± 0.02 | 67.56 ± 0.96 |
| **SWaT** | **92.82 ± 0.19** | 91.77 ± 1.30 | 92.68 ± 0.01 | 92.17 ± 0.05 | OOM |
| **PSM** | 96.34 ± 0.01 | 94.01 ± 0.77 | 95.15 ± 0.14 | 96.31 ± 0.09 | **96.42 ± 0.01** |
| **Avg. F1 (\%)** | **84.44 ± 0.09** | 80.33 ± 1.16 | 81.95 ± 0.25 | 84.07 ± 0.17 | 82.24 ± 0.28 |
Our method consistently retains its advantage in both classification and anomaly detection tasks. We were unable to obtain results for the SWaT dataset using UP2ME (marked with out-of-memory), even after reducing the hyperparameters to manage memory usage.
**Implementation Details:** Based on their official GitHub implementations, only iTransformer has been adapted for classification and anomaly detection. Optimal hyperparameters are provided for iTransformer on 10 UEA datasets and all AD datasets, while for TimeMixer, we used default values for non-forecasting tasks. Hyperparameters for Peri-midFormer are sourced from its GitHub for classification (on 10 UEA datasets) and anomaly detection tasks. Additionally, we test the backbone of UP2ME. We adapted TimeMixer and UP2ME for classification by reshaping the encoder outputs into a one-dimensional vector and passing them through fully connected layers for predictions.
- **Visualizations of Capturing Invariances.**
We will definitely include additional visualizations of the invariances captured by our layers in the revised manuscript. For now, we have included visualizations of offset and trend deformations on UCR datasets, along with feature maps for normal and invariant kernels, in Figures 7 and 8 of the Appendix.
**[Experimental Designs Or Analyses]**
We will incorporate the reviewer's suggestions in the revised manuscript. We already provide extensive details on hyperparameter tuning for the proposed method and the baselines in **Section A.4 Implementation Details**. While results are currently marked based on mean performance and std overlaps, we will consider paired statistical t-tests for all datasets and best methods (not provided due to time constraints). Please also refer to the critical diagram difference for UEA in the rebuttal for **reviewer gvG9**.
**[Clarity]**
> "The mathematics framework is hard [...] intuitive explanations."
To enhance readability, we will relocate Figure 2 to an earlier section of the manuscript to clearly showcase standard deformation types. The methods section will also add a short, intuitive introduction: "The proposed mathematical framework consists of two main components. The first is a group action that formalizes how certain deformations transform time series, resulting in their deformed counterparts. Only deformed time series are observable in practice, such as those influenced by noise or trends. However, embeddings that remain invariant to these deformations are essential for many applications. To address this, the second component is a mapping function that constructs embeddings of deformed time series while remaining invariant to specific deformations. Finally, these embedding maps can be efficiently integrated into convolutional operations to extract robust local features to non-informative deformations.
---
Rebuttal Comment 1.1:
Comment: Thanks for your response. Most of my concerns have been addressed. I will keep my score to support the paper.
---
Reply to Comment 1.1.1:
Comment: Dear reviewer Bfty,
We would like to thank you for your positive feedback on our rebuttal replies. We are grateful for the opportunity to address your concerns, and we are pleased that we have managed to resolve most of the issues raised.
The final version of the manuscript will incorporate the changes and clarifications you suggested, as presented in our rebuttal replies. Specifically, we will include:
*(i)* **Additional runtime comparisons** (beyond the existing ones) between the example architectures and baselines and **visualizations of the learned invariances** for more datasets,
*(ii)* **Performance diagrams with statistical testing** on closely performing methods (such as the one presented in the rebuttal on UEA),
*(iii)* **Results for the four additional recommended baselines** for both classification and anomaly detection, and
*(iv)* **A simple roadmap for the presented mathematical framework** and the considered deformations by relocating relevant figures and providing a more intuitive introduction to the method for a more general audience.
We believe that the above revisions indeed strengthen the manuscript, improving its clarity and impact. We hope *these improvements*, along with *the overall theoretical and methodological contribution of the work*, will help reinforce your positive assessment of the submission even further. We remain happy to provide any last-minute clarification if necessary.
Once again, thank you for your valuable feedback and continued support of our research. | Summary: The article introduces a mathematical framework for integrating invariant into convolution operators for time series. The scaling, offset shifting, and trend invariant are particularly studied. A large number of experiments are then conducted, demonstrating the advantages of these convolutions in terms of their robustness to distortions, their performance in classification, as well as their effectiveness in transfer learning and anomaly detection.
## update after rebuttal
Given the responses provided during the rebuttal, I am increasing my score.
Claims And Evidence: Numerous experiments support the authors' claims regarding the advantage of incorporating hard-coded invariants into convolutions. A first series of experiments artificially introduces distortions to demonstrate the robustness of their method compared to state-of-the-art approaches (Table 1), while comparing results across different types of invariance and convolution. An ablation study is also conducted on classification results to highlight the role of each component (Table 3). Finally, transfer learning experiments are carried out to demonstrate the relevance of the approach in this context.
Methods And Evaluation Criteria: The approach of evaluating the proposed model in two stages is sound, first by introducing artificial distortions and then testing it in real-world conditions. The chosen datasets are standard in the community but known to be simple. The comparison of training times between the different models is also a good aspect. The authors could have produced a synthetic diagram of the model's performance compared to others, such as a mean rank, as is standard in the field. It would have certainly shown slightly lower performance of the proposed model compared to Rocket, as indicated in the exhaustive results table (Table 11) at the end of the appendix, but it could have provided clearer insight for the reader
Theoretical Claims: The article is based on the introduction of an action group for time series. I have read the formalism in detail in the main body of the article and skimmed through the appendices. The formalism is well described and requires some mathematical concepts, not all of which are explicitly stated but remain at a modest level. The examples are well chosen to illustrate the most formal parts.
Experimental Designs Or Analyses: See above.
Supplementary Material: I have only skimmed through the supplementary material.
Relation To Broader Scientific Literature: "To my knowledge, the most important papers in the field are well cited. The authors make a clear effort to position their work in the introduction relative to the state of the art and existing research on invariants for time series. Their proposed idea goes somewhat against the current trend—explicitly designing constraints to integrate into convolutional kernels, whereas the field generally focuses on developing models that can handle invariance in a more generic way. Consequently, the impact of this work may be limited, as there are few real-world cases where invariances are so explicitly defined in my opinion.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: It is unfortunate to limit the study to trend and offset invariants, which can be handled by other approaches. The authors could have discussed other types of invariants to broaden the relevance of their work.
Other Comments Or Suggestions: NA
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We would like to thank the reviewer for the time spent to evaluate our manuscript. We next reply to their key suggestions and comments on our work.
**[Evaluation Criteria]**
>"The authors could have produced a synthetic diagram of the model's performance [...]."
We appreciate the reviewer's suggestion and will add a critical difference diagram, along with clarifying Rocket's first-count performance in the main section. As shown, InvConvNet achieves the best mean rank across 26 UEA datasets and 9 baselines. Using the aeon library [1], we compute mean ranks based on accuracy, confirming significance via a Friedman test (critical difference value of 1.6784 at $\alpha = 0.1$). The Nemenyi post-hoc test identifies three statistically distinct groups: 'InvConvNet' and 'Rocket' in the first, followed by 'TSLANet', 'ResNet', 'TimesNet', 'Cnn', 'Crossformer', and 'PatchTST' in the second.
## Mean Rank for UEA Classification Acc.
| Datasets | **InvConvNet** | TimesNet | PatchTST | Crossformer | TSLANet | DLinear | Inception | ResNet | Cnn | **Rocket** |
|----------------------|----------------|----------|----------|-------------|---------|---------|-----------|--------|-----|-----------|
| *UEA* (26 datasets) | **3.16** | 5.38 | 6.44 | 6.10 | 4.96 | 7.44 | 6.96 | 5.12 | 5.76| **3.68** |
| *CD Value* = 1.6784 | | | | | | | | | | |
[1] https://www.aeon-toolkit.org/en/latest/examples/benchmarking/published_results.html#References
**[Broader Scientific Relations]**
>"Their proposed idea goes somewhat against the current trend [...] few real-world cases were invariances are so explicitly defined in my opinion."
Recent deep learning trends for time series rely on implicit invariances from augmentations using contrastive learning, often lacking generalization guarantees (see Table 1) and incurring high computational costs. Our approach directly encodes common time series invariances within the network, ensuring both efficiency and generalization (see Figure 3, Tables 1 \& 3). Our convolutional design is rooted in group-theoretic modeling of time series deformations, which is a novel approach in this domain. Similar formalisms have introduced robust architectures for computer vision and graph neural networks. Our layers, coupled with lightweight modules (Figures 5, 6), can achieve robust and competitive performance, even on smaller datasets.
**[Other]**
>"It is unfortunate to limit the study to trend and offset [...] discussed other types of invariants."
Baseline removal is common in applications for physiological signals, such as EEGs and PPGs, where baseline wander can mask critical variations, and removing trends can enable more accurate feature extraction [1,2]. The closest easy-to-generate deformation is a smooth random walk, which we incorporate in the robustness experiment as the most complex deformation following simple offset shift and linear trend (see feature maps visualizations in the last row of Figure 8 for smooth random walk deformation of the FordB dataset in Figure 7). Offset shifts and linear trends often arise due to sensor drift, calibration errors, or gradual measurement degradation, leading to misleading variations in the data.
While z-normalization removes global offsets, it fails to address local distortions. Our model learns local invariance to offset shifts and trends, making it effective for real-world data. This justifies our choice of offset shift and linear trend as key deformations to experimentally validate the broader theoretical framework of time series invariant layers under group actions.
In the introduction (paragraphs 4–5, pages 1–2), we discuss time series invariances, including time-shift, time-rescaling, and contrastive learning-based transformations. Commonly addressed deformations include amplitude scaling, offset shifts, and trends, tackled via z-normalization or contrastive frameworks (e.g., TS-TCC). We introduce a formal mathematical framework for time series invariance to spatiotemporal deformations, providing exact formulations of invariances rather than relying on approximations.
We restrict invariant convolutions to simpler but common affine deformations, allowing invariance to trend when it can be assumed linear at the scale of the convolution kernel size. However, we plan to explore approximating the trend with non-linear functions, such as splines or higher-degree polynomials, and incorporating seasonal components with low-frequency cosine bases in future work.
[1] Kaur, M., Singh, B., \& Seema. (2011). Comparing approaches for baseline wander removal in ECG signals. Proc. Int. Conf. \& Workshop on Emerging Trends in Technology, 1290-1294.
[2] Awodeyi, A. E., Alty, S. R., \& Ghavami, M. (2014). On filtering photoplethysmography signals. IEEE Int. Conf. Bioinformatics \& Bioengineering, 175-178.
---
Rebuttal Comment 1.1:
Comment: Thanks for the clarifications, I maintain my score and support acceptance.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer gvG9,
Thank you very much for your thoughtful feedback and the positive evaluation of our work! We are grateful for your support. Your comments have significantly helped to improve the presentation and clarity of our contribution.
Based on our rebuttal, we are committed to incorporating your suggestions by:
*(i)* **Adding performance diagrams** for the proposed method and baselines to further highlight the significance of performance improvements, particularly for the large number of datasets we consider,
*(ii)* **Extending the discussion on practical applications** where invariance to the considered deformations is crucial, and
*(iii)* **Including a discussion on additional complex deformation types** that can be captured by convolutional layers with proper construction (e.g., locally non-linear trends).
We will be grateful for your consideration of these improvements and that of the **additional experiments** in the rebuttal (can be found in reply to **reviewer Bfty**), along *with the overall novelty and multiple contributions of our study* in your final evaluation score.
Once again, thank you for the time you devoted to evaluating our work and for your support. | null | null | null | null | null | null |
Finding Wasserstein Ball Center: Efficient Algorithm and The Applications in Fairness | Accept (poster) | Summary: This paper considers fairness in representing a set of distributions and proposes to use the Wasserstein Ball Centers (WBC) as a representative of a distribution instead of the Wasserstein Barycenter (WB). Given a set of distributions $\mu_1, \ldots, \mu_N$, the Wasserstein Ball Center is defined as a distribution $\mu$ that minimizes the maximum distance to all distributions $\mu_1, \ldots, \mu_N$. Although the definition of WBC seems to be new, as the authors mentioned, the concept of Wasserstein balls is not new.
The main contribution of this paper is in designing an efficient algorithm for computing the WBC of a set of discrete distributions, given a support for the WBC distribution. In particular, they present an IPM-based algorithm that computes the WBC in $O(Nm^3 + N^2m^2 + N^3) time, where $N$ is the number of distributions and $m$ is the support size of each distribution.
## Update after rebuttal
The authors resolved my concerns by adding additional experimental results comparing the disparity scores of their proposed barycenter distribution and the well-known Wasserstein barycenter. I increased my score from 3 to 4.
Claims And Evidence: The Theorems and Lemmas are clear.
Methods And Evaluation Criteria: I have concerns with the fairness evaluation criteria, as the only criterion used for measuring the fairness of the proposed method is the maximum distance of each group to the representative distribution (which is exactly the objective function that the WBC tries to minimize). It is not surprising to have lower maximum Wasserstein distance of each group to WBC compared to WB, and although one of the metrics for computing fairness is the maximum distance, many other metrics need be used to show better fairness of the proposed method over WB.
I understand that the authors claim the main contribution of their paper to be the design of fast algorithms for computing WBC; however, since the authors provide experiments on comparing the fairness of their method compared to WB, they would need to provide more evidence on that front to consider it an added value to the paper.
Theoretical Claims: I checked some of the proofs, and they seem to be correct. I have a problem with the construction of b, and I would appreciate it if the authors would let me know whether I am missing something.
In the construction of the matrix A, the first M + Nm rows check the mass preservation of the transport plans. Then there is a 1_m, which is supposed to check that the total mass of w is 1. The next N rows ensure that gamma_i's are properly defined; *here, I think there is a missing 1_N in the vector b*.
Experimental Designs Or Analyses: The experimental results show some benefits of the proposed method over the Gurobi solver. I have some questions about the experiments on the running times (experiment 1):
How did you form the distributions? What are the dimensions of the distributions? Are they all supported on the same support? How did you choose the support of the WBC?
Supplementary Material: I reviewed some parts of the supplementary materials, including the experiments and the algorithms.
Relation To Broader Scientific Literature: The Wasserstein barycenter is a widely used method for representing a set of distributions and has found applications in numerous scientific fields. However, it might not be the fairest representation as it might be far from some under-represented groups. This paper suggested the use of WBC instead to resolve the fairness and provided an algorithm for computing WBC.
Essential References Not Discussed: No
Other Strengths And Weaknesses: The main weakness of the presented work is that the paper assumes that the support of the WBC is already given. It is not clear at all how one can derive this support set, and it is not the same as the support of the distributions. For instance, suppose we have three distributions in 2D, each one supported on a single point, forming a triangle. Then, one needs to take points inside this triangle while forming the WBC.
Other Comments Or Suggestions: No
Questions For Authors: I asked my questions in previous sections.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1** On the missing part of the vector $\boldsymbol{b}$.
We sincerely appreciate the reviewer’s meticulous reading. Yes, there is a missing $\boldsymbol{0}_N$ as the last $N$ terms of vector $\boldsymbol{b}$. We will correct this typo in the final version. Notebly, since the design of our algorithm focuses on the constraint matrix $A$, this typo does not affect any other part of the paper.
**Q2** About the experiments on the running times (experiment 1): How did you form the distributions? What are the dimensions of the distributions? Are they all supported on the same support? How did you choose the support of the WBC?
For the first three question, see Line 403-405 in paper: "we generate random datasets in $\mathbb{R}$, and the weights of $(q_1^{(t)}, ..., q_m^{(t)})$ in each distribution $P^{(t)}$ are generated uniformly at random."
The support points of the WBC is generated in the same way, and we will clarify this in the final draft. Thank you for pointing out this ambiguity.
**Q3** About the fairness metric in paper
We sincerely appreciate your valuable suggestion, which highlights the need for a more comprehensive discussion of fairness in the context of WBC.
One of the inspirations of this paper is the *social fairness* concept as mentioned in the last paragraph of Introduction and Appendix A. Apart from that, *Minimax fairness* is gaining increasing attention within the machine learning community [1-3], where fairness is achieved by minimizing the maximum error across groups—as opposed to minimizing the average error (i.e., replacing $\min\sum$ with $\min\max$ in the objective). This aligns precisely with our formulation.
We acknowledge that there are other fairness notions—such as demographic parity [4], equalized odds/opportunity [5-6], and individual fairness [7]. Extending these frameworks to probability-measure spaces (e.g., via Wasserstein metrics) presents a compelling direction for future research, and we will include a brief discussion of this in the revised manuscript.
**Q4** How can one derive this support set, and it is not the same as the support of the distributions?
Due to space limitations, please refer to our response to **Q2** of Reviewer f8bo to view block coordinate descent method. As for our point-cloud experiment (see Appendix I.3), we proceeds as follows:
1. **Initialization**: Compute the fixed-support WBC using the vertices of a dense grid as the initial support set.
2. **Support Update**:
- *Augmentation*: Sample new points from Gaussian distributions centered at high-weight support points.
- *Pruning*: Remove support points with negligible weights (below a threshold).
3. **Iteration**: Recompute the fixed-support WBC on the updated support and repeat until convergence.
This design is motivated by two key observations:
- The WB admits a sparse support representation, with a theoretical upper bound of $N\max\limits_{i\in [N]}m_i$ [8].
- Adaptive refinement balances computational efficiency with solution accuracy by dynamically focusing on high-density regions, which avoid too many iterations.
From the theoretical perspective, "free-support WBC'' is indeed a much more challenging problem than the fixed-support case, especially when the dimensionality is high. We further note that even the ``fixed-support WB'' problem is also very hard and the polynomial-time algorithm with high precision is only for fixed-dimension [8]. We appreciate the reviewer for raising this question, and will spend more effort to investigate this problem as the future work.
[1] Martinez, Natalia, Martin Bertran, and Guillermo Sapiro. "Minimax pareto fairness: A multi objective perspective." *International conference on machine learning*. PMLR, 2020.
[2] Abernethy, Jacob D., et al. "Active Sampling for Min-Max Fairness." *International Conference on Machine Learning*. PMLR, 2022.
[3] Singh, Harvineet, et al. "When do minimax-fair learning and empirical risk minimization coincide?." *International Conference on Machine Learning*. PMLR, 2023.
[4] Zemel, Rich, et al. "Learning fair representations." *International conference on machine learning*. PMLR, 2013.
[5] Hardt, Moritz, Eric Price, and Nati Srebro. "Equality of opportunity in supervised learning." *Advances in neural information processing systems* 29 (2016).
[6] Woodworth, B., Gunasekar, S., Ohannessian, M., and Srebro, N. (2017). Learning non-discriminatory predictors. In Proceedings of the 2017 Conference on Learning Theory, pages 1920–1953.
[7] Dwork, Cynthia, et al. "Fairness through awareness." *Proceedings of the 3rd innovations in theoretical computer science conference*. 2012.
[8] Altschuler, Jason M., and Enric Boix-Adsera. "Wasserstein barycenters can be computed in polynomial time in fixed dimension." *Journal of Machine Learning Research* 22.44 (2021): 1-19.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their thorough response.
Concerning the fairness metric, there exist some other fairness metrics, such as the Disparity Impact as the variance or range of the distances of the distributions to the barycenter and the Normalized Disparity Score.
I also believe that to compare the fairness, the experiments can be enhanced a lot by considering more meaningful distributions in higher distributions rather than 1D uniform distribution.
---
Reply to Comment 1.1.1:
Comment: **Q1** About other fairness metric.
Thank you for your insightful suggestion regarding additional disparity impact analysis, and we will incorporate further discussion and experiments on this topic to the final manuscript. Here, we conducted some preliminary experiments to compare the variance of the Wasserstein distances from the input distributions to the WBC (denoted as $\textrm{var}(d_{WBC})$) and that of the WB (denoted as $\textrm{var}(d_{WB})$). Below are the settings in our experiment:
- Ground space dimensions: 3, 10 and 100.
- Ground metrics: $L_1, L_2$, and $L_\infty$.
- Support selection regimes: Uniform sampling in a cube, Gaussian sampling. Both composed with cluster-diversifying transformations (which divide the support points into 1, 2 or 3 clusters).
For each parameter combination of above three categories, we test 50 different instances (2700 total instances). Each instance contains 30 distributions with uniform sampled weights, and each distribution has support size 200. In *all* 2700 instances, $\textrm{var}(d\_{WBC}) < \textrm{var}(d\_{WB})$, indicating that **$\text{var}(d\_{WBC})$ is usually smaller than $\textrm{var} (d\_{WB})$.** For example, in $L\_1$ space of dimension 100, we sample the 30 supports uniformly in a cube with side length 3, then translate 3 supports by adding $-\boldsymbol{1}\_{100}$, and translate 5 supports by adding $2*\boldsymbol{1}\_{100}$, run algorithms to obtain that $\textrm{var}(d\_{WBC})=58.35$, while $\textrm{var}(d\_{WB})=418.61$. Those observation suggests that WBC not only improves fairness for the minority distributions, but also could enhance fairness *across all distributions* by limiting disparities between transport plans. To further explain this phenomenon, we will explore the theory of the inherent property of transport plans to WBC in future work.
**Q2** Test other distributions in higher dimensions to compare fairness.
Thanks for your suggestion. In our paper, the fairface experiment (Section 4(3)) and the pointcloud experiment (Section 4(4)) showcases the fairness performance of WBC in real-world data distributions in $\mathbb{R}^2$ and $\mathbb{R}^3$. Here, we further conduct a set of additional experiments in higher dimension that generalise the "fairness of WBC" experiment in Section 4(2). The experimental distributions are partitioned into two families, where the supports of family 1 are sampled from normal distributions centered at $5*\boldsymbol{1}\_d$ and those in family 2 are sampled from normal distributions centered at $-5*\boldsymbol{1}\_d$, $d$ is the dimension of ground space. To quantify the disparity between these two families, define the imbalanced factor ("imf'') as the ratio of the first family's size to the second one. Results are listed in table 1-3. The results demonstrate fairness on those distributions in higher dimension, and we will include more experiments of high dimension in the final manuscript.
Table 1: fairness in $L_2$ space of dimension 100. We notice that the magnitude defference between $\textrm{var}(d_{WBC})$ and $\textrm{var}(d_{WB})$ is big. This phenomenon may be related to properties of normal distributions in high-demonsional space, and will be studied later.
| imf | 0 | 0.2 | 0.4 | 0.6 | 0.8 | 1 |
| ------------- | ----- | ------ | ------ | ------ | ------ | ----- |
| Max WD of WBC | 48.24 | 281.25 | 301.41 | 228.64 | 228.42 | 194.52 |
| Max WD of WB | 61.54 | 578.70 | 548.55 | 447.46 | 292.54 | 218.15 |
|$\textrm{var}(d_{WBC})/10^{-9}$| 8.76| 56.50|63.22|53.28| 64.89|54.81|
|$\textrm{var}(d_{WB})/10^3$|8.54| 7.51| 26.41|36.21|9.20|5.67|
Table 2: fairness in $L_2$ space of dimension 1000.
| imf | 0 | 0.2 | 0.4 | 0.6 | 0.8 | 1 |
| ------------- | ----- | ------ | ------ | ------ | ------ | ----- |
| Max WD of WBC$/10^3$ | 1.44 | 1.48 | 1.47 | 1.46 | 1.51 | 1.45 |
| Max WD of WB$/10^3$| 1.85 | 2.75 | 2.11 | 1.87 | 1.84 | 1.79|
|$\textrm{var}(d_{WBC})/10^{-10}$| 6.84| 14.50|7.26|11.04| 5.18|4.41|
|$\textrm{var}(d_{WB})/10^4$|5.13| 27.55| 32.48|41.50|9.21|16.61|
Table 3: fairness in $L_2$ space of dimension 10000.
| imf | 0 | 0.2 | 0.4 | 0.6 | 0.8 | 1 |
| ------------- | ----- | ------ | ------ | ------ | ------ | ----- |
| Max WD of WBC$/10^4$ | 1.25 | 1.35 | 1.41 | 1.37 | 1.32 | 1.30 |
| Max WD of WB$/10^4$ | 1.54 | 1.90 | 1.75 | 1.60 | 1.43 | 1.48 |
|$\textrm{var}(d_{WBC})/10^{-10}$| 8.76| 5.54|6.06|13.26| 4.88|4.81|
|$\textrm{var}(d_{WB})/10^4$|3.54| 7.19| 31.24|46.20|40.25|11.38|
We also supplement the runtime analysis in Section 4(1) with high-dimensional experiments, which will be discussed in detail in the final manuscript.
Table 4: When $N=30, d=1000$, running time (s) as the support size $m$ varies.
|m /100| 1|2|3|4|5|6|7|
|---|--|---|--|--|--|--|--|
|Ours|4.56 |5.42| 11.07| 12.49| 26.15 |30.83|35.81|
|Gurobi| 17.11|53.21|410.02| 726.84| 1650.14|Null | Null| | Summary: This paper introduces the concept of "Wasserstein Ball Center" (WBC) as an alternative to the traditional Wasserstein Barycenter (WB) for finding a representative probability distribution from multiple input distributions. While WB minimizes the sum of Wasserstein distances from the barycenter to all input distributions, WBC minimizes the maximum Wasserstein distance to any input distribution. This "minmax" approach makes WBC more fair to "minority" distributions that differ significantly from the majority.
The main contributions are:
Formulating the WBC problem as finding the center of the minimum-radius ball that covers all input distributions in Wasserstein space
Showing that the fixed-support WBC problem can be formulated as a large-scale linear programming (LP) instance
Developing an efficient interior point method (IPM) to solve this LP problem by exploiting structure in the constraint matrix to achieve significant speed improvements over standard approaches
Demonstrating through experiments that WBC provides more equitable treatment of outlier distributions compared to WB
The authors' algorithm accelerates the IPM by O(min{N²m, Nm², m⁴}) times compared to vanilla IPM, where N is the number of distributions and m is the support size. Experiments on both synthetic and real datasets show that their algorithm is more computationally efficient than commercial solvers and that WBC indeed provides more fair representation for minority distributions.
Claims And Evidence: The paper's claims are generally well-supported by evidence:
1. The theoretical claims about computational complexity improvements are supported by detailed mathematical derivations and proofs that exploit the structure of the linear programming formulation.
2. The fairness advantage of WBC over WB is demonstrated through:
- Visual examples showing how WBC preserves characteristics of outlier distributions (Fig. 1)
- Quantitative results showing reduced maximum Wasserstein distance for minority distributions (Fig. 3b)
- Case studies using the FairFace dataset showing more equitable treatment across racial groups
- 3D point cloud visualization showing how WBC preserves features from minority shapes
The computational efficiency claims are validated by comparing runtime performance against the Gurobi commercial solver, with clear advantages demonstrated across various problem scales.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand:
1. The paper provides a sound mathematical formulation of the WBC problem as a linear program, which is a natural approach for solving the proposed minmax optimization.
2. The interior point method (IPM) with specialized matrix manipulations is an appropriate choice for this problem, as it exploits the specific structure of the constraint matrix.
3. The evaluation criteria are well-chosen: Computational efficiency is measured against a strong baseline (Gurobi solver)
Theoretical Claims: The paper contains several theoretical claims and proofs, particularly around the computational complexity of their algorithm and the structure of the constraint matrix in the proposed LP formulation.
The main theoretical result is Theorem 3.2, which states that the time complexity of each inner iteration of the IPM is O(m²∑ᵢmᵢ + Nm³ + N²m² + N³), and the memory usage is O(m∑ᵢmᵢ + Nm² + N²).
The proof of this theorem is built on several intermediate results:
Proposition 3.1 (showing the constraint matrix can be made full row-rank)
Proposition 3.4 (describing the structure of the normal equation matrix)
Proposition 3.5 (further decomposing the structure of specific submatrices)
Lemma 3.6 (providing an efficient way to compute a key matrix inverse)
Experimental Designs Or Analyses: The experimental designs and analyses in the paper are sound:
Compare the proposed algorithm against Gurobi, a state-of-the-art commercial solver
Evaluate performance with varying N (number of distributions) and m (support size)
Measure both computation time and objective value
Demonstrate super-linear convergence rate (Fig. 3a)
Supplementary Material: The supplementary material supports the claims made in the main paper. The detailed proofs provide necessary mathematical foundations for the theoretical results, and the additional experiments demonstrate the robustness of the findings across different settings.
Relation To Broader Scientific Literature: The paper builds upon and extends several areas in the scientific literature:
Wasserstein Barycenter
Fairness in Machine Learning
Optimal Transport
Essential References Not Discussed: The paper is generally thorough in its literature review, but a few relevant references might strengthen the connections:
Recent advances in fast approximation algorithms for Wasserstein distance computation. For exmaple (https://arxiv.org/abs/2312.01432)
Some recent work on fair Wasserstein barycenters (e.g., weighted schemes that give more importance to minority groups) could provide interesting contrast to the proposed minmax approach.
Other Strengths And Weaknesses: Strengths:
The paper addresses an important problem - the inherent bias in Wasserstein barycenters against minority distributions - with a principled mathematical approach.
The experimental results convincingly demonstrate both computational efficiency and fairness benefits across differents scenarios.
The paper connects theoretical optimal transport concepts with practical fairness implications, especially in domains like medical imaging where fairness is crucial.
Weaknesses:
The paper focuses primarily on the discrete, fixed-support case. Some discussion on how the approach might extend to continuous distributions or free-support problems would strengthen the work.
The paper could provide more guidance on choosing between WB and WBC for different applications - when is the fairness benefit of WBC worth potential increases in average Wasserstein distance?
The computational improvements, while significant, are still limited by the inherent complexity of the LP formulation. For very large-scale problems, approximation methods might be necessary. (https://arxiv.org/abs/2312.01432)
The experimental evaluation could benefit from more downstream tasks to show how the improved representation of minority distributions impacts practical applications.
Other Comments Or Suggestions: NA
Questions For Authors: How does the proposed WBC approach handle noisy distributions or outliers that might not represent meaningful minorities but rather data corruption?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: **Q1:** Missing references
Thank you for your valuable suggestions on the references, and we will add them to the revised version.
**Q2:** Algorithm for free-support Wasserstein ball center (WBC)
For the free support Wasserstein barycenter, many previous researches [1-3] apply block coordinate descent. For our WBC, we can also utilize this approach, where the objective becomes:
\\[
\begin{array}{cl}
& \min\limits_{\boldsymbol{w}, X, \left\\{ \Pi^{(t)} \right\\}} \max\limits_{t\in [N]} \left\langle D(X,Q^{(t)}), \Pi^{(t)} \right\rangle \\\\
\text{s.t.} & \Pi^{(t)} \boldsymbol{1}_{m_t} = \boldsymbol{w}, \left( \Pi^{(t)} \right)^{\top} \boldsymbol{1}_m = \boldsymbol{a}^{(t)}, \Pi^{(t)} \geq 0, \forall t = 1, \cdots, N \\\\
& \boldsymbol{1}_m^{\top} \boldsymbol{w} = 1, \boldsymbol{w} \geq 0
\end{array}
\\]
where $\boldsymbol{w} := (w_1, \cdots, w_m)^{\top} \in \mathbb{R}_+^m$, $X:= [\boldsymbol{x}\_1, \cdots, \boldsymbol{x}\_m] \in \mathbb{R}^{d \times m\_t}$, $\Pi^{(t)} \in \mathbb{R}\_+^{m\times m\_t}$ and $D(X, Q^{(t)}):= [ \\| \boldsymbol{x}_i - \boldsymbol{q}^{(t)}_j \\|^p ]\in \mathbb{R}^{m \times m_t}$ for $t=1,\cdots, N$.
Free support WBC is nonconvex. By block coordinate descent, one optimizes the support set $X$, and then the fixed support WBC to obtain the weight $\boldsymbol{w}$ of WBC and coupling matrices $\Pi^{(t)}$ alternately. The algorithm will converge to a local minima. For instance, in $l_2$ space, the minimization of $X$ is $\min\limits\_{X}\max\limits\_{t\in [N]}\sum\_{k=1}^m\sum\_{j=1}^{m\_t}||\boldsymbol{x}\_k-\boldsymbol{q}\_j^{(t)}||^2\pi\_{kj}^{(t)}$. This is a quadratically constrained quadratic program (QCQP) in that it can be reformulated as the following problem:
\\[
\begin{aligned}
&\min\limits\_{X,\zeta} \zeta \\\\
\text{s.t.} \ \ &\sum_{k=1}^m\sum\_{j=1}^{m_t}||\boldsymbol{x}\_k-\boldsymbol{q}\_j^{(t)}||^2\pi\_{kj}^{(t)}\leq \zeta
\end{aligned}
\\]
Since the quadratic forms of $X$ in the constraints is positive semidefinite, the problem is convex [4], thus can be efficiently solved with convex programming, such as interior point method. Note that the size of variable $X, \zeta$ is $m+1$, the number of constraints is $N$, the scale of solving $X$ is much smaller than solving the fixed support WBC.
Due to space limitations, please refer to our response to **Q4** of Reviewer YCD8 for our approach in the point-cloud experiment (see also Appendix I.3).
From the theoretical perspective, "free-support WBC'' is indeed a much more challenging problem than the fixed-support case, especially when the dimensionality is high. We further note that even the ``fixed-support WB'' problem is also very hard and the polynomial-time algorithm with high precision is only for fixed-dimension [5-6]. We appreciate the reviewer for raising this question, and will spend more effort to investigate this problem as the future work.
**Q3:** Provide more guidance on choosing between WB and WBC for different applications - when is the fairness benefit of WBC worth potential increases in average Wasserstein distance?
Thanks for this question, and we will include a discussion on it. In general, the trade-off between **fairness** (WBC) and **average performance** (WB) depends on the application:
- **WBC** is preferable when minimizing *worst-case deviation* is critical (e.g., equitable resource allocation).
- **WB** is better for applications where *average accuracy* dominates (e.g., density estimation).
**Q4:** How does the proposed WBC approach handle noisy distributions or outliers that might not represent meaningful minorities but rather data corruption?
Thank you for raising this interesting question. Please see the answer to **Q2** in response to Reviewer Xncv.
[1] Cuturi, Marco, and Arnaud Doucet. "Fast computation of Wasserstein barycenters." *International conference on machine learning*. PMLR, 2014.
[2] Ge, Dongdong, et al. "Interior-point methods strike back: Solving the wasserstein barycenter problem." *Advances in neural information processing systems* 32 (2019).
[3] Huang, Minhui, Shiqian Ma, and Lifeng Lai. "Projection robust Wasserstein barycenters." *International Conference on Machine Learning*. PMLR, 2021.
[4] Floudas, Christodoulos A., and Viswanathan Visweswaran. "Quadratic optimization." *Handbook of global optimization* (1995): 217-269.
[5] Altschuler, Jason M., and Enric Boix-Adsera. "Wasserstein barycenters can be computed in polynomial time in fixed dimension." *Journal of Machine Learning Research* 22.44 (2021): 1-19.
[6] Lin, Tianyi, et al. "Fixed-support Wasserstein barycenters: Computational hardness and fast algorithm." Advances in neural information processing systems 33 (2020): 5368-5380. | Summary: This paper considers the following problem: Given a set of N probability measures, find a probability distribution that, minimizes the maximum distance to any input distribution. Intuitively, we can think of this as the problem of finding the center and radius of the “smallest Wasserstein ball” that encloses all the input distributions. A closely related problem is the Wasserstein barycenter problem where the objective is to minimize the sum total of the Wasserstein distances from the center to the $N$ distributions. While Wasserstein barycenter has been extensively studied, there is (to my knowledge) nothing known about solving the smallest Wasserstein ball problem.
Similar to the Wasserstein barycenter, if we assume that the support for the center is fixed, then one can formulate the exact problem as an LP and use standard methods to solve the problem. The authors make some interesting observations that gives this LP a simpler structure resulting in a faster exact algorithm using IPM for the problem. The overall execution time of their algorithm is $O(Nm^3+ N^2m^2+N^3)$ as opposed to $O(N^3m^4)$ using vanilla IPM.
The authors apply this novel optimization problem as a means to achieve fair centers to represent the distributions including those that may be underrepresented. The authors implement their solutions and show that they outperform state-of-the-art LP solvers (such as gurobi). They also provide some evidence on the impact of their approach on the problem of fairness.
Rebuttal Update: Thank you for your response. I will keep my positive score.
Claims And Evidence: All claims are supported by proofs.
Methods And Evaluation Criteria: The authors show the benefits of proposed algorithm (in terms of time and memory usage) with a gurobi implementation. This is a solid comparison. The experiment to highlight fairness seems like a reasonable one.
Theoretical Claims: I have skimmed through the proofs presented in the main text and I did not find any issues with them.
Experimental Designs Or Analyses: Yes. The experimental set up seems sound to me.
Supplementary Material: I did not review any of the supplementary materials.
Relation To Broader Scientific Literature: The problem studied is novel and I'm not aware of any paper that directly addresses the algorithmic question of computing the smallest Wasserstein ball for fixed support. However, the problem is similar to the classical 1-center problem (perhaps the discrete 1-center problem because of the fixed support requirement) in Wasserstein metric. Since 1-center for arbitrary metric spaces is extensively studied, perhaps adding a comparison of your work with that would be good.
Essential References Not Discussed: I did not find any missing references.
Other Strengths And Weaknesses: Overall, the optimization problem considered here is novel and a very natural question to study. The result provided is interesting both from a theoretical standpoint as well as from an empirical standpoint.
My main concern that the paper does not address is the sensitivity of the objective function to the presence of an outlier distribution. A single outlier distribution can disproportionately shift the center towards the outlier. Due to this, I worry that the actual practical value of the optimization problem in real-world may be limited. Could the authors comment on this?
Other Comments Or Suggestions: NA
Questions For Authors: Please address the concern raised in strength/weakness section.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Q1:** Comparison between our work and 1-center problem for arbitrary metric space.
Thanks for the question regarding the connection between our WBC problem and the 1-center problem in arbitrary metric spaces. We will add more references and explanations in our paper. In Euclidean space, 1-center problem is often called “minimum enclosing ball problem'' or ”minmax location problem''. Their numerical or approximate algorithms has been extensively studied, see [1-5]. However, the 1-center problem under Wasserstein metric remains unexplored—precisely the gap our work aims to address. Due to the inherent nature and complexity of Wasserstein metric, those previous 1-center algorithms cannot be directly applied to handle our proposed WBC problem (to our best knowledge).
**Q2:** How to deal with outlier distributions?
Thank you for raising this interesting question. Actually, we think it is hard to precisely distinguish between "outlier'' and "minority'', if there is no any prior knowledge/assumption. For example, a minority distribution could be far away from other distributions, and thus performs quite similarly as an outlier. So we believe an efficient way should take some prior knowledge on inliers and outliers into account.
When no prior information is available, we can also utilize the following iterative strategy to extract "outlier'' distributions and construct the WBC for the remaining distributions (which is similar with the "trim'' idea in statistics): initially, we compute the WBC of the input distributions; perform the following two steps in each iteration, until stable:
1. Recognize the set of distributions farthest from the current WBC as outliers;
2. Update the WBC as the WBC of the remaining distributions.
Nevertheless, since we do not have any prior knowledge, the above strategy could bring some error (e.g., mistaken a minority distribution as an outlier). So we believe it deserves more further study on how to distinguish between "outlier'' and "minority'', and which kinds of prior knowledge can be utilized.
[1] Bâdoiu, Mihai, and Kenneth L. Clarkson. "Smaller core-sets for balls." Proceedings of the fourteenth annual ACM-SIAM symposium on Discrete algorithms. 2003.
[2] Tansel, B.Ç. (2011). Discrete Center Problems. In: Eiselt, H., Marianov, V. (eds) Foundations of Location Analysis. International Series in Operations Research & Management Science, vol 155. Springer, New York.
[3] Abboud, Amir, et al. "On Complexity of 1-Center in Various Metrics." *Approximation, Randomization, and Combinatorial Optimization. Algorithms and Techniques* (2023).
[4] Yildirim, E. Alper. "Two algorithms for the minimum enclosing ball problem." *SIAM Journal on Optimization* 19.3 (2008): 1368-1391.
[5] Kumar, Piyush, Joseph SB Mitchell, and E. Alper Yildirim. "Approximate minimum enclosing balls in high dimensions using core-sets." *Journal of Experimental Algorithmics (JEA)* 8 (2003): 1-1. | null | null | null | null | null | null | null | null |
Average Certified Radius is a Poor Metric for Randomized Smoothing | Accept (poster) | Summary: This paper studies the shortcomings of Aversage Certified Radius (ACR) as a performance metric for randomized smoothing. It shows theoretically that this metric can be “hacked” by a trivial classifier with an arbitrarily large certified radius on a small number of “easy” input points, thereby achieving SOTA performance under this metric. It confirms this theoretical finding empirically by designing model training strategies that discount hard input samples, prioritize easy samples, and put more weight on higher certified radii. Based on its findings, it argues for the discontinuation of ACR as a metric for evaluating randomized smoothing-based robustness techniques.
Claims And Evidence: 1. The paper argues that ACR is not a proper metric for evaluating randomized smoothing. However, most works in this field do not use ACR as the sole evaluation metric. The primary evaluation metric is certified accuracy at different values of the certified radius. This metric does not have the shortcomings of the ACR metric. Even the two works cited by this paper to argue that ACR is being used by the community continuously only use ACR as a secondary evaluation metric together with certified accuracy. Thus, the paper’s claim that ACR “has emerged as the most important metric for comparing methods and tracking progress in the field” is debatable.
2. The theoretical claims regarding a trivial classifier achieving infinite ACR by over-optimizing on easy samples have been validated with short proofs of correctness. However, the theoretical claims are straightforward and not very surprising. Please see my comments under “Theoretical Claims”.
Methods And Evaluation Criteria: The paper proposes three modifications to training with Gaussian noise, namely discarding hard inputs, reweighting samples with approximate certified radius and attacking the noised samples, to develop a new method to achieve state-of-the-art performance under the ACR metric. This method shows that improving the ACR metric is indeed possible without actually making the model more robust. However, the method only achieves marginal improvements in ACR over existing methods, as shown in Table 2.
Theoretical Claims: Proofs of theorems 1 and 2 are both correct. However, as mentioned earlier, these theorems are straightforward and the insights are unsurprising. Theorem 1 formalizes that a trivial classifier can achieve an arbitrarily high ACR by simply predicting the most likely class for all inputs, thereby having infinite certified radii for samples for this class and blowing up the ACR metric. Theorem 2 merely states that two points with the same L_2 norm have the same probability density under an isometric Gaussian distribution.
Experimental Designs Or Analyses: The experiments and analyses are reasonable for showing the weaknesses of the ACR metric.
Supplementary Material: The supplementary material provides code for the experimental evaluations. I have not checked the code in great detail.
Relation To Broader Scientific Literature: I am unaware of other works that study the weaknesses of evaluation metrics for certified robustness.
Essential References Not Discussed: Several well-known works in this field do not use ACR as their evaluation metric. For instance, [1] and [2] evaluate the certified robustness of RL agents using metrics such as certified reward, which does not suffer from the weaknesses of ACR. The paper should include more examples of works in the field and discuss the metrics used by them to give the reader a better understanding of how commonly the ACR metric is used as the primary evaluation metric in the literature.
[1] CROP: Certifying Robust Policies for Reinforcement Learning through Functional Smoothing, Wu et al, ICLR 2022.
[2] Policy Smoothing for Provably Robust Reinforcement Learning, Kumar et al, ICLR 2022.
Other Strengths And Weaknesses: Strengths:
1. The paper is clearly written and easy to understand.
2. It provides theoretical and empirical evidence to justify that ACR is a poor metric for randomized smoothing.
Weaknesses:
1. The claim “the average certified radius (ACR) has emerged as the most important metric for comparing methods and tracking progress in the field” is not well substantiated. Please see my comments under “Claims And Evidence” and “Essential References Not Discussed.”
2. The theoretical claims lack originality. Please see my comments under “Theoretical Claims”.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank Reviewer $\Rg$ for the insightful review. We are happy that Reviewer $\Rg$ finds that our paper is easy to understand, and that our work provides both theoretical and empirical evidence to justify our conclusion. We address all concerns from Reviewer $\Rg$ below. We include new results, named with Figure S1 etc., in the [anonymized link](https://mega.nz/file/2NtyHIpA#EcvgiAMI7xMjXTgcGHnVpWdg-U2QnojAPVqF7peCMwM).
**Q1: ACR is rarely used as a stand-alone metric. Is the claim that “ACR is the most important metric” proper?**
We agree that claiming ACR is the most important metric is improper. To gain quantitative insights, we perform a literature survey in RS for publications on top conferences (ICML, ICLR, AAAI, NeurIPS), ranging from 2020 (since the first evaluation with ACR) to 2024. We only include works that use the certification algorithm proposed by Cohen et al. and propose general-purpose dataset-agnostic RS algorithms. We identify 13 works with the specified criteria, and report for each of them (1) whether ACR is evaluated, (2) whether universal improvement in certified accuracy is achieved at various radii, (3) whether a customized base model is used (either parameter tuning or architecture design) and (4) whether claims SOTA. The result is shown in Table S4.
Among them we find 10 works that customize the model and claim SOTA, which is the focus of our study. 8 of them evaluate with ACR, and 7 of them claim SOTA solely based on ACR, i.e., claim SOTA without universal improvement in certified accuracy at various radii. Therefore, we conclude that ACR is of great importance to the field, and the practice of claiming SOTA based on ACR is widely spread. We will incorporate this study in the revised manuscript and revise the statement about the role of ACR accordingly.
**Q2: The method proposed in this paper only has a marginal improvement on ACR compared to state-of-the-art (SOTA) approaches. Does this weaken the conclusion?**
Our finding is that simply focusing on easy samples with the proposed Algorithm 2 replicate the progress in RS training strategies. Therefore, our method is **not** designed to achieve great advances in ACR further; instead, it is to prove how unreliable the evaluation of ACR could be. Therefore, we do not view the relatively small improvement over SOTA as a limitation of this work.
**Q3: The theoretical analysis is straightforward and unsurprising. Does it mean that the paper lacks originality?**
We agree that the theoretical analysis is straightforward but kindly disagree that it is unsurprising. First, to the best of our knowledge, this analysis has never been done before, leaving the weakness of ACR unknown yet. As a result, ACR is still widely adopted in RS training, as discussed in Q1. Second, the theoretical analysis serves as a crucial foundation for our empirical analysis and motivates our proposal to abandon ACR as the central metric for evaluating RS training algorithms. Therefore, we kindly disagree with the claim that our theoretical analysis lacks originality or significance. | Summary: This paper critiques the use of Average Certified Radius (ACR) as an evaluation metric for assessing the performance of certifiably robust classifiers, specifically focusing on randomized-smoothing-based approaches for robustness certification under the $\\ell_2$ perturbation threat model.
(To give background: in an $\\ell_2$-certifiably-robust classifier, for each input sample $x$, the classifier both returns a classification $\\hat{f}(x)$ as well as a radius $R(x)$, such that for any $x'$ such that $\\|x-x'\\|_2 < R(x)$, the sample $x'$ is guaranteed to be classified in the same way as $x$: that is, $\hat{f}(x) = \hat{f}(x')$. Typical randomized smoothing approaches (for the $\\ell_2$ metric) compute $\hat{f}(x)$ by taking the plurality-vote of the output of a _base classifier_ $f(x + \delta)$ on many noise instances $\delta$ drawn from an isometric Gaussian distribution: the certified radius $R(x)$ is then computed as a (monotonically increasing) function of $p_A$, the fraction of noise instances $\delta$ on which $f(x + \delta)$ retuned the plurality class.)
As an evaluation metric, the Average Certified Radius is defined on a labelled test set $(x_1, y_1), ..., (x_m,y_m)$ as:
$$
ACR = \\frac{1}{m} \\sum_{i=1}^m \\begin{cases} R(x_i) & \\text{ if } f(x_i) = y_i, \\\\ 0 & \\text{ otherwise. }\\end{cases}
$$
The paper claims that ACR is commonly used to evaluate randomized-smoothing based certifiably robust classifiers. The paper then notes (Theorem 1) that ACR can be ``gamed'' to be made arbitrarily large: specifically, a _constant_ function $\hat{f}(x) = c$, which classifies all samples with the same class c, combined with a certification technique that (_correctly_) reports an arbitrarily large certified radius R(x) for each sample (note that these certifications are correct, because the classification function $\hat{f}(x)$ is constant) will have an arbitrarily large ACR as long as *any* samples in the test set are labeled as c. In particular, this set-up can be instantiated using standard randomized smoothing certification techniques, by using a constant base classifier, and a sufficiently-large number of smoothing samples to make R(x) as large as desired.
In practice, in randomized smoothing (RS) certification techniques, the certified radius R(x) is *capped* by a function of the number of smoothing samples $\delta$ used, and hence by the certificate computation time. However, the paper goes on to claim that in RS techniques, training design choices that increase ACR tend to increase the certified radii R(x) of the "easiest" samples in the data distribution (those which already have a large certified radius) at the expense of "harder" samples. This phenomenon is demonstrated empirically by comparing the cumulative certified radius distribution of Cohen et al. (2019), one of the first RS techniques, with the cumulative certified radius distributions from more-recent works, on CIFAR-10 (Figure 6; Table 2). For small radii r, Cohen et al's method is more likely to correctly classify samples and certify them as robust to radius R(x) >= r, while for large radius r, the more recent techniques prevail. The paper explains this phenomenon theoretically as being due to the fact that the certified radius R(x) grows very quickly as a function of $p_A$ when $p_A$ is near 1 ( and $R(x)$ is already large ), while growing much more slowly with $p_A$ when $p_A$ and $R(x)$ are small. Therefore increasing the certified radii of "easy" samples even further is "easier" than increasing the certified radii of "hard" samples by the same amount, because it requires increasing $p_A$ of the "easier" samples by a much smaller increment.
The paper goes on to design a training method for certifiably robust classifiers that is designed to "game" ACR as much as possible (practically; without increasing the number of smoothing samples). They propose to skip "hard" samples during training, weight training samples by "easiness," and adversarially choose smoothing perturbation vectors $\\delta$ during training to ensure that $p_A$ is as close to 1 as possibly for "easy" samples. The resulting classifiers have state-of-the-art ACR on CIFAR-10 and relatively-low clean accuracy (although not the lowest among certifiably-robust methods.
Finally, the paper suggests alternatives to using ACR to evaluate certifiable robustness: reporting the cumulative distribution of R(x) (that is, the fraction of test samples which are correctly classified and have $R(x) \geq r$ for various values of $R$) as well as the distribution of $p_A$.
Claims And Evidence: The basic argument that ACR alone provides an incomplete picture of certifiable robustness, because it can be made arbitrarily high by using a trivial (constant) classifier, is correct, and the proof of the associated Theorem 1 is correct.
However, the submission claims that:
"Randomized smoothing is a popular approach for providing certified robustness guarantees against adversarial attacks, and has become an active area of research. Over the past years, the average certified radius (ACR) has emerged as the **most important** metric for comparing methods and tracking progress in the field." [Abstract] (emphasis added)
"Average Certified Radius (ACR), defined to be the average of the certified radiuses over each sample in the dataset, has been **the main metric** to evaluate the effectiveness of these methods" [Introduction, Lines 31-33] (emphasis added).
These claims are not well-supported. While the paper does cite six works which report ACR as a metric, the following additional context is relevant and is not mentioned:
- **None** of the works report ACR _alone_ as the sole metric for comparing RS techniques; all of them also give the cumulative distribution of R(x).
- All but two of the cited works which use ACR share the same first-author, showing that the use of this statistic is less wide-spread than is suggested by the total number of provided references.
- Several works which deal with $\\ell_2$ certifiable robustness via randomized smoothing, which do not use ACR, were not mentioned. This includes works which propose new techniques, such as:
Awasthi et al. "Adversarial robustness via robust low rank representations", NeurIPS 2020
Zhang et al. "Black-Box Certification with Randomized Smoothing: A Functional Optimization Based Framework" NeurIPS 2020
Li et al. "Double Sampling Randomized Smoothing" ICML 2022
as well as survey papers which compare many proposed techniques, and do **not** report ACR, such as:
Li et al. "SoK: Certified Robustness for Deep Neural Networks" IEEE SP 2023
Furthermore, the claims in the Abstract and Introduction sections highlighted above are not qualified as being only about $\\ell_2$ certifiable robustness, although later it is stated that " In this work, we focus on the L2 neighborhood of an input," (Background, lines 66-67). The cited examples of ACR are all papers about L2 certified robustness, and no examples are given outside of this specific line of work. However, many papers exist which use randomized smoothing-based techniques and do not report ACR. (See the above survey for examples of certification results for other metrics.) Therefore the general claim made in the abstract that "Randomized smoothing is a popular approach [...] the average certified radius (ACR) has emerged as the **most important** metric for comparing methods and tracking progress in the field" is not supported by evidence provided in the paper. To properly evidence this claim, one would need to perform a much wider and more objective meta-analysis of all literature in randomized smoothing. (Note that even if *every* paper using randomized smoothing reported ACR, this would not justify the claim that ACR is the *most important* metric for comparing methods.)
Additionally, while the experimental evidence does seem to justify that, for fixed smoothing noise standard-deviation $\sigma$, newer RS methods tend to increase the certified robustness of "easy" samples at the expense of accuracy on "hard" samples (at least on CIFAR-10), the experimental comparison includes SmoothAdv (Salman et al. 2019), which does not report ACR, but which seems to behave similarly in terms of the shape of the certificate distribution to the methods which do, at least compared to Cohen et al (2019). This seems to undermine the **causative** claim in the abstract that "Overall, our results suggest that ACR has introduced a strong undesired bias to the field."
The other claim that this paper makes that I do not believe is sufficiently justified is the relevance of the theoretical argument made in Section 4.2; specifically, the claim that "We have shown that ACR strongly prefers easy samples in §4.2." (line 155-156) The issues with this claim are elaborated below under "Theoretical Claims."
Methods And Evaluation Criteria: The methods and evaluation appear to be sound; however, only CIFAR-10 was used in the experiments. It would be better to include a dataset with more natural images (for example ImageNet, or, if that is not feasible, an ImageNet subset).
Theoretical Claims: The main theoretical claim in the paper (that ACR can be unbounded for trivial classifiers), Theorem 1, is correct and has a correct proof.
Theorem 2 is a minor technical result, which is not of great importance to the paper. However, its proof is only correct as written if we interpret $P_{\\mathcal{N}(0,\\sigma^2I_d)}(\\delta)$ to refer to the probability _density_ at $\delta$. This notation is not explained, and conflicts with the notation in the Background section, where $P_{\\delta \\sim \\mathcal{N}(0,\\sigma^2I_d)}(f(x+\\delta) = c)$ refers to the _probability_ (not the density) of the event. The text at line 305-306: "This is because for every δ∗such that ∥δ∗∥2 = ∥δ0∥2, the probability of sampling δ∗is the same as δ0. We formalize this fact in Theorem 2." should also be revised: "the probability of sampling δ∗" is _infinitessimal_.
A major theoretical over-claim in this work is that: "We have shown that ACR strongly prefers easy samples in §4.2." (line 155-156). The theoretical argument in Section 4.2 shows that the certified radius R(x) grows very quickly as a function of $p_A$ when $p_A$ is near 1 ( and $R(x)$ is already large ), while growing much more slowly with $p_A$ when $p_A$ and $R(x)$ are small. Therefore, it is suggested that algorithms which are tuned to increase average radius will tend to increase p_A for samples where p_A is already large, because this will have a greater impact on average radius than an equal increase in p_A for samples where p_A is small. However, this theoretical observation alone does *not* establish, as implied, that it is "easier" to increase the certified radius of a sample with p_A near 1 than a sample with a lower p_A. Concretely, while it is true that increasing p_A from .99 to .999 increases R(x) by a much larger margin than increasing p_A from .6 to .609, it is not obvious that it is _as easy to increase_ p_A from .99 to .999 as to increase p_A from .6 to .609. In fact, one can make a compelling theoretical argument for the opposite: that it should be much harder to increase p_A from .99 to .999 than to increase p_A from .6 to .609.
Specifically, due to the nature of the high-dimensional Gaussian distribution, the minimum _volume_ around $x$ for which the base classifier $f(x+\\delta)$ must return class A in order to achieve $p_A = .999$ is much larger than the minimum volume around $x$ that must belong to class A in order to achieve $p_A = .99$, and in particular, this gap in minimum-volumes is much larger than the gap between the volumes required to achieve $p_A = .6$ and $p_A = .609$. (To help understand this, note that achieving p_A = 1 _requires_ that $f$ is constant _everywhere_). Therefore an analysis in terms of $p_A$ alone is perhaps misleading, and does not fully "show that ACR strongly prefers easy samples".
The empirical evidence _does_ seem to suggest that the methods with the highest ACR tend to focus on increasing p_A for "easier" samples; however, I think it is an over-claim to say that the argument in Section 4.2 fully explains the phenomenon: more nuance is required.
Experimental Designs Or Analyses: One confusion I had with the experimental design was the explanation of Figure 3 in line 193: " As a result, Gaussian training has higher P(pA ≥0.5) (clean accuracy)," Clean accuracy is not the same as p_A >= 0.5. If there are more than two classes, samples can be labeled correctly by the smoothed classifier with p_A < 0.5; they just won't get a certified radius by Cohen et al's method. It would be good to also label the _actual clean classification accuracy_ of each classifier. (For example, if the classifiers are classifying samples correctly, with radius 0)
Additionally, throughout the paper, it is implicitly assumed that we are using the empirical certification algorithm described in Cohen et al, which only bounds the probability $f(x+\delta)$ returning the ``top'' class. For example, on Line 137-138: " Further, when pA < 0.5, the data point will not contribute to ACR at all," Some methods can in fact certify when p_A < 0.5, such as the method used in (Lecuyer et al, 2019; Dvijotham et al., "A Framework for robustness Certification of Smoothed Classifiers using F-Divergences" ICLR 2020). This should be clarified.
Supplementary Material: The proofs were checked.
Relation To Broader Scientific Literature: This paper provides concrete suggestions to future researchers in randomized smoothing for certified adversarial robustness, specifically:
1. To avoid using ACR (Average Certified Radius) as a metric for robustness.
2. To instead report the highest-achievable certified accuracy at specified radii.
3. To report the cumulative distribution of p_A for the test set.
For (1) the paper does establish that at least some prior works do report ACR, and then shows how this statistic can be vacuous; furthermore, I am not aware of any prior works that explicitly point out these issues with ACR. However, it is not well-established that the use of ACR is as common as claimed ("the most important metric") . Additionally, as noted above, (2) is already done _nearly-universally_ in prior works. Furthermore, (3) may be somewhat limited: if methods differ in terms of _how_ they compute certificates given $p_A$, then (3) does not allow for a fair comparison (for example: Li et al. "Double Sampling Randomized Smoothing" ICML 2022); additionally, (3) does not allow for comparison to non-RS certified robustness methods. Furthermore, p_A is not actually relevant to downstream applications: it is an internal metric of the certification process.
Essential References Not Discussed: See the above discussion. While, to my knowledge, this is the first work to explicitly identify that ACR is a problematic metric, there are many works in this space that do not use ACR but were not cited. To restate some examples given above:
Awasthi et al. "Adversarial robustness via robust low rank representations", NeurIPS 2020
Zhang et al. "Black-Box Certification with Randomized Smoothing: A Functional Optimization Based Framework" NeurIPS 2020
Li et al. "Double Sampling Randomized Smoothing" ICML 2022
Li et al. "SoK: Certified Robustness for Deep Neural Networks" IEEE SP 2023
There are many more such works in existence; a more comprehensive survey is needed to assess whether ACR is truly a ubiquitous metric.
Other Strengths And Weaknesses: Strengths:
- The main argument of the paper, that ACR is not an appropriate metric on its own, because it may be vacuous, is compelling and is argued correctly.
- While this was not the stated aim of this paper, it appears from the results that the proposed training method (for fixed $\sigma$) did achieve a higher certified accuracy at large radii than all prior works, at least on CIFAR-10. This training method can then be seen on its own as an additional contribution.
Other Comments Or Suggestions: Minor Comments:
Line 34-35: "Although some studies refrained from using ACR in their evaluation unintentionally" -- It is not knowable whether on not this was "intentional"; it would be better to say "Although some studies have not used ACR (without mentioning a justification for this choice)"
Line 44: "Due to the incompleteness of adversarial attacks ": I think this means that adversarial attacks only prove an upper bound on the true robustness/distance to the decision boundary, but this is not worded clearly.
Line 31" "radiuses" -> radii
Line 96: "is commonly used" -> "was commonly used"
Equation on line 94: The sum is meaningless here, and so can be omitted: we're taking the average over m identically-distributed samples, within an expectation. The sum can be commuted with the expectation, where it then becomes clear that all of the summands are equal.
Line 106: "While they all improve ACR" -> "While these methods all improve ACR"
Line 134-135: "with minimal robustness on at least half of classes." Why not minimal robustness on all but one class?
Lines 138-139: "since inputs with lower pA require a larger budget to certify. " : This seems to be an oversimplification. On the contrary, isn't the certified radius most sensitive to the estimated probability, and hence to sampling budget, when pA is near 1? (The example given in this paragraph shows a more complex relationship)
Line 160: "We follow the standard certification setting in the literature, setting N = 10^5 and α = 0.001." : I believe these parameters are originally from Cohen et. al. 2019; I would cite them.
Section 4.2 (and Figure 2): I believe this figure is showing the relationship between the _measured_ p_A (from samples) and the certified radius. However, p_A is actually defined as the _population average_ in line 79 in Section 3. This should be clarified.
Table 1: is this _parameter_ gradient or _feature_ gradient magnitude?
Line 319-321: "Therefore, with the adaptive attack, Gaussian training obtains a similar gradient norm distribution to SOTA algorithms": I would no longer call the proposed method, with the adaptive attack, "Gaussian training"
"Furthermore, the community should also consider randomized smoothing methods with σ as a variable rather than a hyperparameter, thus effectively removing the dependence on σ. While there are some preliminary works in this direction (Nurlanov et al., 2023), they usually break the theoretical rigor, thus more research is needed in this direction." Nurlanov et al is not a relevent citation (it does not use randomized smoothing.) There are works in this direction, however, as noted, there are issues with correctness in many of these works. see (Sukenik et al,"Intriguing Properties of Input-Dependent Randomized Smoothing" ICML 2022) for further discussion.
Use of capital I for both identity matrix and indicator function is confusing; would use bold 1 instead for indicator function.
Proof of Theorem 1: the proof seems to implicitly be using binomial (Clopper-Pearson) confidence interval; I would be more explicit about it.
Questions For Authors: - Is there any _quantitative evidence_ that the _proportion of published randomized smoothing papers which use ACR_ is above 50\%? If so, how many use ACR alone?
- Does the observed trend apply to datasets other than CIFAR-10?
++++++++++++++++++++++
Both questions were responded to during rebuttal period: I am increasing my score to 'Weak accept'.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank Reviewer $\Rn$ for the insightful review. We are happy that Reviewer $\Rn$ finds our work is important and valuable, and points out imperfect expressions. We will address all the concerns raised by Reviewer $\Rn$ in the following. We include new results, named with Figure S1 etc., in the [anonymized link](https://mega.nz/file/2NtyHIpA#EcvgiAMI7xMjXTgcGHnVpWdg-U2QnojAPVqF7peCMwM).
**Q1: Is ACR the most important metric in the community? Is there any quantitative evidence which supports their claim?**
Please refer to our reply to Q1 of Reviewer $\Rg$.
**Q2: SmoothAdv, which is before the invention of ACR, has similar issues as presented in this paper. Does this undermine the claim that ACR introduced a strong undesired bias to the field?**
We agree that although the empirical evidence in Sec 4.3 shows that a strong bias is introduced to the field, it does not directly imply that ACR is the only reason. In fact, the hypothesis that ACR has causality with the bias is not provable. Therefore, we will temper our tone and state that “A strong bias has been introduced to the field, which is highly likely due to the practice of claiming SOTA based on ACR given the demonstrated properties”.
**Q3: Could the authors clarify notations in Theorem 2 and the text at 305-306 rc?**
We thank Reviewer $\Rn$ for pointing out the notation conflicts. We will define the notations more clearly and replace the infinitesimal probability with PDFs of the Gaussian function in the revised manuscript.
**Q4: Easier samples contributing much more to ACR than harder ones does not imply that it is easier to improve $p_A$ of easy samples than hard ones. Is the claim that ACR strongly prefers easy samples proper?**
We agree that more contribution from easy samples does not directly imply that focusing on easy samples will increase ACR. We refer to our reply to Q3 of Reviewer $\Ru$ for a detailed discussion. However, the claim that ``ACR strongly prefers easy samples`` simply states that easy samples contribute more, but does not conclude that focusing on easy samples will increase ACR. Nevertheless, to avoid confusion, we will adjust this statement properly.
**Q5: Do the results generalize to other datasets?**
Please refer to our reply to Q1 of Reviewer $\Rp$.
**Q6: Does this work assume applying the certification algorithm described in [1]?**
Yes. In fact, we only discuss works that are based on the certification algorithm in [1] since the subject is RS training strategies but not certification algorithms. We will clarify this in the revised manuscript.
**Q7: Could the authors clarify the definition of clean accuracy when not using the prediction algorithm of [1]?**
We consider the certification method in [1], which does not provide a prediction if the empirical $p_A$ is below 0.5 (i.e., the algorithm returns ABSTAIN). In this case, the clean accuracy is defined as the accuracy at a certified radius of 0. This convention is also adopted in previous works such as [1, 2, 3].
As a future reference, we additionally report the accuracy of different methods when the model performs a majority vote without abstaining in Table S3. It shows that without abstaining the clean accuracy is always marginally higher than that with abstaining. The result without abstaining is consistent with the analysis in this work performed with abstaining.
**Q8: For the proposed metric, the cumulative distribution of $p_A$, can it be used to compare different certification algorithms? How to use it for downstream applications?**
As discussed in Q6, this work focuses on the certification algorithm proposed by [1]. However, cross-certification evaluation is still possible. Appendix B thoroughly discusses how to convert the distribution of $p_A$ into certified accuracy at different radii and different budgets. If comparisons of different certification algorithms are desired, then based on methods discussed in appendix B.1, one may first convert it to certified accuracy before comparison. This is more flexible than certified accuracy at fixed budget, because different certification might vary in certification budget. Similarly, for downstream applications, since the proposed metric is more generalized than certified accuracy, it allows more flexible evaluation; importantly, every evaluation that is based on certified accuracy can be recovered cheaply based on the distribution of $p_A$. Nevertheless, this metric is only meaningful for $p_A$-based certification; it must be converted into other metrics to compare with other certification algorithms. We will clarify these aspects in the revised manuscript.
Reference
[1] arxiv.org/abs/1902.02918
[2] arxiv.org/abs/1906.04584
[3] arxiv.org/abs/2212.09000
---
Rebuttal Comment 1.1:
Comment: Thank you for your response. The additional, systematic literature review is helpful and the results on ImageNet are also appreciated. I am raising my score on the strength of these additional results. (I also expect that the over-claim about ACR being the "most important" metric will be revised in the final draft, as promised; and for the final draft to more clearly state that the work is _only_ concerned with training methods for Cohen et al.'s certification scheme, not Randomized Smoothing in general.)
For Q2 above, I would directly call out the fact that SmoothAdv does not use ACR, but shows the same trend, in the paper.
I don't think that the response to Q4 really answered my concerns. It is not clear what "easy samples contribute more" in the response means: ACR is an unweighted average, so each sample contributes the same. The argument in Section 4.2 concerns the _marginal_ effect of a small _increase_ of $p_A$ on ACR. I pointed out that this argument may have little relevance to ACR, because increasing $p_A$ on any "easy" sample by a given $\epsilon$ may be much more difficult than increasing $p_A$ on a "hard" sample by the same $\epsilon$. In fact, we might expect this to be the case, because the additional volume of $f$ that must be near-constant around $x$ to increase $p_A$ from $0.99$ to $0.99 +\epsilon$ is much greater than the additional volume of $f$ that must be near-constant around $x$ to increase $p_A$ from $0.6$ to $0.6 +\epsilon$. Therefore a theoretical analysis in terms of $p_A$ alone is incomplete. (The response to uKgY which was cited does not mention Section 4.2 at all, which is what my question was about.)
Regarding Question 7: Cohen et al propose _two_ algorithms: PREDICT and CERTIFY. PREDICT returns the classification of a sample, while CERTIFY gives a certified radius. Both algorithms can abstain. However, while CERTIFY will always abstain of $\hat{p}_A < 0.5$, PREDICT does not necessarily abstain when there is no majority class: as long as as there is a sufficient gap between the top class and the runner-up class, PREDICT will return the top class (the winner of the plurality vote.) Based on this scheme, the "Clean Accuracy" should refer to the accuracy of PREDICT, which is distinct from either the fraction of samples for which $\hat{p}_A \geq 0.5$ *or* the "no abstain" top class.
---
Reply to Comment 1.1.1:
Comment: We thank Reviewer $\Rn$ for the insightful reply and for appreciating our additional literature study and experiments. We are happy to provide further discussion on Q4 and Q7.
**Further discussion on Q4**
It seems that Reviewer $\Rn$ refers to different aspects from ours. We believe that Reviewer $\Rn$ refer to the fact that the derivative of ACR to each radius is the same ($1/n$), but we refer to the fact that the derivative of ACR to $p_A$ is dramatically large when $p_A$ is close to 1. We may further improve the writing clarity regarding this aspect.
**Further discussion on Q7**
We may further clarify the aspects about clean accuracy since different readers may have different interpretations about this in the context of RS and Cohen’s prediction algorithm.
We thank Reviewer $\Rn$ for their efforts in evaluating our work. We hope our reply has fully addressed their concerns. | Summary: The authors make a strong claim that the Average Certified Radius (ACR) - which is widely used through the Randomized Smoothing (RS) community - is not a good metric at all for a number reasons. They prove it, and provide the ways how it can be exploited for improving ACR.
## update after rebuttal
Authors provided the asked additional experiments (even for ImageNet), so I keep my original score.
Claims And Evidence: Claims:
* Theoretic proof that ACR can be arbitrarily large even for a trivial classifier, esp. when its improvement is rooted in easy examples
* Empirical justification of the current RS training strategies intention to concentrate on easy examples (with high $p_{A}$)
* Based on theoretical and empirical observations, the authors proposed the specific methods to improve the existing RS training strategies (Section 5) by a) discarding hard examples during training, b) training examples re-weighthing with Certified Radius, and c) adjusting the perturbation to have the same norm but broking the classifier (they called it "Adaptive Attack")
Overall, the approach by authors can be formulated as following:
1. They empirically and theoretically investigated on why the ACR is a bad metric
2. They exploited their observations to produce the best (SotA) defense methods
3. They proposed what could be the better metric instead of ACR (Section 7 - e.g., using the best certified accuracy at various radii or use $\sigma$ as a variable, not a hyperparameter)
Methods And Evaluation Criteria: All the proposed methods (already existing and adopted in the community of RS researchers as well as the new one proposed in Appendix B for constructing the Empirical CDF for $p_{A}$) sound solid and reasonable.
As for the datasets itself, CIFAR-10 was used - which is quite widely used for the task of RS. Unfortunately, no ImageNet results were delivered - which would provide a stronger message about this paper.
Theoretical Claims: Yes, the authors provided the proof of the Theorem 1 (about arbitrary high ACR) in Appendix A1, as well as the auxiliary simple proof for the Theorem 2 (about the probabilities of the equal norm perturbations). While looking simply the theorems are carefully proved.
Moreover, inside the Appendix B.1 there is a description (while not explicitly theoretically formulated but still rigorous) of the procedure to convert ECDF($p_{A}$) to ECDF($r_{cert}$) with different value of $N$ which is very well described.
Experimental Designs Or Analyses: Actually, two main remarks:
1. No usage of other than CIFAR-10 dataset. ImageNet was used even in the seminal paper of [1].
2. There is no re-estimation of the existing RS defenses for the metrics proposed in Section 7. Yes, there is a slight approach in the Appendix B, but it is definitely not enough. If the paper proposes the new way of measuring Certified Robustness for RS, than it makes to provide the new measurements of the methods and see how they compare against each other - whether the order is different etc
[1] Cohen, J. M., Rosenfeld, E., and Kolter, J. Z. Certified adversarial robustness via randomized smoothing. In Proc. of ICML, volume 97, 2019.
Supplementary Material: Yes, all.
Relation To Broader Scientific Literature: The whole paper is devoted to the certified robustness through probabilistic approach - randomized smoothing. RS is the main method to assess certification of deep NNs.
Essential References Not Discussed: NA
Other Strengths And Weaknesses: To me, very well organized paper with the structure: Observation --> Exploitation --> Proposal to change.
Would be nice to address the items mentioned in "Experimental Designs Or Analyses"
Other Comments Or Suggestions: I'm not quite sure if it is a typo or some my misunderstanding of the following sentence in Section 7:
"this represents the setting where one first fixes an interested radius, and then try to develop the best model with the highest certified radius at the pre-defined radius."
Questions For Authors: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank Reviewer $\Rp$ for the insightful review and faithful interpretation of our work. We are happy that Reviewer $\Rp$ finds our work important, sound and solid. We will resolve all the concerns below. We include new results, named with Figure S1 etc., in the [anonymized link](https://mega.nz/file/2NtyHIpA#EcvgiAMI7xMjXTgcGHnVpWdg-U2QnojAPVqF7peCMwM).
**Q1: Do the results generalize to ImageNet?**
Yes. We perform a new analysis on ImageNet, generalizing the findings presented in this work. Concretely, Figure S1 is an extension of Figure 3 on ImageNet, and Table S1 is an extension of Table 2 on ImageNet. The hyperparameters used in the study are reported in Table S2. We find that all our conclusions remain correct on ImageNet, justifying their generalization across datasets.
**Q2: Could the authors extend the evaluation of previous works using the proposed “ECDF of $p_A$” metric?**
Sure. The ECDF of $p_A$ on CIFAR-10 with different $\sigma$ and algorithms are shown in Figure S2. We note that an algorithm is better only if it has higher ECDF for all $p_A \ge 0.5$. Therefore, it is possible that neither of two algorithms is better than the other.
For various $\sigma$, Gaussian is always the best in the low $p_A$ region, i.e. from $p_A=0.5$ to around 0.65. Although CAT-RS consistently has the highest ACR under all $\sigma$, it only outperforms other methods in the high $p_A$ region. For example, with $\sigma=0.5$, CAT-RS is the second worst method when $p_A$ is below 0.74. We list some cases where two methods have strict orders: with $\sigma=0.25$, CAT-RS is better than Consistency and SmoothAdv; with $\sigma=0.5$, CAT-RS is better than SmoothMix; with $\sigma=1.0$, CAT-RS is better than SmoothMix and MACER.
**Q3: Clarification of the typo in Sec. 7.**
Thanks for pointing out the typo. It should be "try to develop the best model with the highest **certified accuracy** at the pre-defined radius".
---
Rebuttal Comment 1.1:
Comment: I would like to thank authors for making additional experiments and addressing my remarks about experimental part.
While the curves look similar, I'm a little bit concerned about the Table 2 in the anonymized link. It seems that a list of your "exploitation" techniques like "Discard Hard Data During Training", "Data Reweighting with Certified Radius", and "Adaptive Attack on the Sphere" is mostly overfitted on CIFAR-10 - because for ImageNet, the ACR (that should be the best for your approach) is now even not the second biggest one for high $\sigma$. It makes the sections of "Replicating the Progress in ACR" in the original paper look questionable.
Looking forward to any insights about it.
---
Reply to Comment 1.1.1:
Comment: We thank Reviewer $\Rp$ for the quick reply and their effort in reading our new experimental analysis; their comments have been constructive and encouraging. We are glad to provide further discussion about Table S1 below.
The relevant claim made in this manuscript is that simply focusing on easy samples is enough to replicate the advances in RS training strategies. We agree that while on CIFAR-10 the proposed modification to Gaussian training achieves SOTA ACR universally, on ImageNet it only replicates a large portion of the ACR advances. Concretely, for $\sigma=0.25$, the proposed method recovers (0.529 - 0.476) / (0.532 - 0.476) = 94.6% of the advance; for $\sigma=0.5$, it recovers (0.842 - 0.733) / (0.846 - 0.733) = 96.5%; for $\sigma=1$, it recovers (1.042 - 0.875) / (1.071 - 0.875) = 85.2%. Therefore, it is confirmed that the same evidence is found on ImageNet. To be more precise, we will change the claim to “simply focusing on easy samples is enough to replicate the advances in RS training strategies, sometimes even surpassing existing SOTA algorithms”.
Further, there are complex reasons why our preliminary results on ImageNet provided in the initial rebuttal do not surpass SOTA, and more efforts may further improve it. First, on ImageNet CAT-RS utilizes a pre-trained model [1] to determine the inclusion of certain loss terms, which is not used on CIFAR-10. This improves the result of CAT-RS on ImageNet, while our preliminary results even skipped “Data Reweighting with Certified Radius” to deliver fast results. Second, we did not conduct a sufficient hyperparameter search on ImageNet due to time reasons in the initial rebuttal, while a good tuning is performed on CIFAR-10. Despite these challenges, our proposed method still recovers most of the advances on ImageNet. Therefore, we believe that this proves the generalization of our results across the dataset. In the final manuscript, we will apply more computation on ImageNet and check if similar tricks using a pre-trained model may be applied for our method, e.g., use the pre-trained model to determine the hardness of inputs throughout training rather than using $p_A$ computed on-the-fly. This should further improve our preliminary numbers, with the potential to also establish SOTA ACR on ImageNet. We also would like to note that due to the arguments made in this manuscript, achieving SOTA ACR is less meaningful, and our current results are sufficient to support our claims.
Reference
[1] arxiv.org/abs/2212.09000 | Summary: The authors investigate the validity of the Average Certified Radius (ACR) as a measure for robustness.
Claims And Evidence: Claims and Evidence:
C1. Authors theoretically show that with a large enough certification budget, ACR of a trivial classifier can be arbitrarily large, and that with the certification budget commonly used in practice, an improvement on easy inputs contributes much more to ACR than on hard inputs, more than 1000x in the extreme case.
E1. One of the evidence for this claim provided by the authors is Theorem 1. I am not convinced of this result being meaningful. Indeed a constant classifier is trivially the most robust classifier by any measure of robustness. And Theorem 1 formalizes this intuition. But this type of analysis is fundamentally flawed in the methodology: simultaneously optimizing two objectives is not the same as optimizing both of them separately. That is optimizing only robustness will not lead to the same solution as the one when optimizing for robustness and accuracy together.This analysis does not take into account predictive performance of the classifier, and any real-world robustness training algorithm will optimize for both robustness and accuracy.
## Update after rebuttal: The authors correctly pointed out my misjudgment of the theorems results, and I think there analysis is correct and meaningful.
C2. ACR disproportionately focus on easier examples, i.e., samples with more confident predictions (and hence larger p_A) are disproportionately represented in ACR. However, the authors also claim that this leads to potentially poorer RS algorithms (which I do not agree with, see below).
E2. As ACR is essentially an average, where the weights are the proportional to CDF of a normal distribution at $p_A$, it indeed over-represents samples with larger $p_A$. However, in section 4.3, I do not agree with the analysis. The authors criticize the fact that the RS training procedures "lowers the $p_A$ for harder samples" --- I do not understand why they should behave otherwise? I would argue that the user should see a lower $p_A$ for harder samples, this does not contradict the fact that ACR can be misleading, but claiming that this has lead to wrong RS algorithms is misleading.
## Update after rebuttal: I think the situation is clearer to me now. And I think the point about "selection bias" seems valid.
C3. The authors show that focusing only on easier samples can improve ACR.
E3. Authors provide an algorithm and experimental evaluation to this end. However, I think this fact is clear, as ACR is a weighted average as mentioned above. See "Experimental Designs Or Analyses".
## Update after rebuttal: My statement was wrong, and the authors are indeed correct to provide experimental evidence for gaming ACR.
Methods And Evaluation Criteria: Authors provide theoretical results, and verify them experimentally, with an algorithm to produce the misleading ACR behavior, on widely known benchmark datasets and RS.
Theoretical Claims: See above in "Claims and Evidence" section
Experimental Designs Or Analyses: I think the experimental design is sound, but it is also tautological, i.e., the hypothesis they are testing is not falsifiable by the experiments they are performing. In my understanding, given the definition of ACR, and then discarding hard samples one will provably improve ACR.
## Update after rebuttal: I think this assessment was indeed incorrect and my understanding of the paper has been improved by looking at section 4.2 again, and reading the author's discussion with Reviewer nJsf.
Supplementary Material: I briefly looked at proof of Theorem 1.
Relation To Broader Scientific Literature: The main message of the paper is potentially very relevant to RS research, depending on how widely ACR is used as a metric.
However, I think ACR is a misleading metric only if it is used as a stand-alone metric.
The fundamental point of the paper can be boiled down to the fact that average, and hence ACR, is not a robust statistic.
## Update after rebuttal: I think this assessment is indeed correct to a large extent.
Essential References Not Discussed: None, to the best of my knowledge.
Other Strengths And Weaknesses: Strengths:
The key message of the paper is potentially very important.
Weakness:
Almost all of the peripheral analysis is potentially misleading.
The main message should just be that average is not a robust statistic and one should not base metrics for safety-critical applications on that.
## Update after rebuttal: I would like to retract my comments about the "misleading analysis". However, I still believe that the main result indeed, in large parts, can be attributed to averages not being robust statistics.
Other Comments Or Suggestions: -- I am quite ambivalent about the paper, on one hand I think the key message of the paper is pertinent. However, as described above, I find many points raised in the paper to be rather misleading (in my understanding).
## Update after the rebuttal: As mentioned earlier, I do not think anymore that the analysis is misleading, barring the fact that ACR still does not seem to be the most important metric
Questions For Authors: -- Why cant the entire message of the paper be summarized in the fact that ACR is average of the radii, and averages can be arbitrarily moved by just moving one instance, and hence ACR can be made arbitrarily good by just focusing on easy samples with large robustness radii?
-- What is the usefulness of Algorithm 2? as one can see from definition of ACR focusing too much on easy samples will indeed improve it. Is Algorithm 2 verifying this point?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: $\newcommand{\Ru}{\textcolor{green}{uKgY}}$
$\newcommand{\Rp}{\textcolor{blue}{Ptgp}}$
$\newcommand{\Rn}{\textcolor{fuchsia}{nJsf}}$
$\newcommand{\Rg}{\textcolor{purple}{gJ9M}}$
We thank Reviewer $\Ru$ for the insightful review. We are happy that Reviewer $\Ru$ finds our work important and experiments sound. In the following, we will address all concerns raised by Reviewer $\Ru$. We include new results, named with Figure S1 etc., in the [anonymized link](https://mega.nz/file/2NtyHIpA#EcvgiAMI7xMjXTgcGHnVpWdg-U2QnojAPVqF7peCMwM).
**Q1: Does the robustness in this paper (especially Thm 1) consider both predictive performance and output stability under small input perturbation?**
Yes. As defined in 68-69 rc, the robustness defined in this work considers both the predictive performance and the output stability. Specifically, Thm 1 also considers both aspects, and inputs that are mistakenly predicted will not contribute to ACR. Furthermore, Reviewer $\Ru$ claims that ``a constant classifier is the most robust classifier by any measure of robustness``; this is not true. For example, under our definition of robustness, a constant classifier can have zero robustness: consider a dataset that only contains class 0 for a binary classification task, then a constant classifier predicting class 1 will have zero robustness (and zero ACR). We hope this classifies the misconception about our definition of robustness.
**Q2: Why shouldn’t RS training lower $p_A$ for harder samples?**
The term ``harder samples`` in Sec 4.3 refers to samples with $p_A$ larger than but close to 0.5, and ``easier samples`` refers to samples with $p_A$ close to 1. Therefore, as shown in Sec 4.3, if RS training is justified to lower $p_A$ for harder samples, then under small radii (e.g., $r=0$), the certified accuracy of “better algorithms” will be **lower** than “worse algorithms”, contrary to the intuition.
In addition, the claim made in Sec 4.3 is not “this has led to wrong RS algorithms”; instead, we claim that this introduces selection bias (that “better algorithms” have worse certified accuracy under small radii) into the development of RS algorithms, as explicitly stated in the title of Sec 4.3. The latter is directly supported by empirical evidence.
**Q3: Given the definition of ACR, will ACR be provably improved by focusing on easy samples? Is the hypothesis “focusing on easy samples improves ACR” trivially true and does not require empirical evidence in this work? What is the main goal of Algorithm 2?**
The hypothesis is not trivially true. While an improvement on $p_A$ of any input without a decrease on $p_A$ of other inputs leads to increased ACR, it is not guaranteed that improving $p_A$ of easy samples does not reduce $p_A$ of hard samples. In fact, as shown in Sec 4.3, the reverse is usually true. Thus, ACR is not provably increased by focusing on easy samples. Further, the hypothesis will only hold when the benefits of improvement on easy samples exceed the loss on hard samples. This leads to our experimental analysis in Sec. 5 and 6 based on Algorithm 2. The main goal of Algorithm 2 is to both validate this hypothesis and the second hypothesis that the progress in RS training strategies can be replicated by simply focusing on easy samples.
**Q4: Is ACR really misleading, as it is rarely used as a stand-alone metric?**
Please refer to our reply to Q1 of Reviewer $\Rg$.
**Q5: Can the entire paper be summarized “ACR is average of the radii, and averages can be arbitrarily moved by just moving one instance, and hence ACR can be made arbitrarily good by just focusing on easy samples with large robustness radii”?**
This summary is partially true, but misrepresents important scopes established in this work. It is true that ACR is the average of the certified radius, and averages can be arbitrarily moved by an infinite change on only one instance. However, as pointed out in our reply to Q3, this does not directly prove that ACR can be made arbitrarily good by just focusing on easy samples with large radii. In fact, our empirical results in Sec. 6 shows that ACR can at least be amplified to the state-of-the-art (SOTA) by focusing on easy samples, but still not infinitely large. As discussed in Q3, there might exist an equilibrium where the loss on hard samples exactly offsets the improvement on easy samples, leading to maximized ACR. The more accurate summary of this work should be: (i) ACR is problematic because it does not faithfully represents the robustness and it is much more sensitive to the same magnitude of improvements on easy samples than hard samples, (ii) empirical evidence shows that ACR of Gaussian training can be amplified to SOTA by simply focusing on easy samples, and (iii) ACR should be replaced by better alternatives such as certified accuracy at various radii and the ECDF of $p_A$ when evaluating RS training strategies. | null | null | null | null | null | null |
The Case for Learned Provenance-based System Behavior Baseline | Accept (poster) | Summary: This paper proposes a new ML method for anomaly detection in provenance graphs. The results demonstrate the effectiveness of the proposed method.
Claims And Evidence: The claims and assumptions as well as the evaluation metrics are reasonable to me.
Methods And Evaluation Criteria: The proposed method is well presented.
Theoretical Claims: The paper does not have a theoretical claim.
Experimental Designs Or Analyses: The experiment design is comprehensive in general and the results are impressive. I would suggest adding experiments on transformers if possible.
Supplementary Material: I read through it.
Relation To Broader Scientific Literature: This paper advances the field of ML-based anomaly detection, an important and practical domain.
Essential References Not Discussed: I would suggest the authors discuss more existing works on anomaly detection, e.g., CADE [USENIX'21].
Other Strengths And Weaknesses: The paper is well written.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your review efforts and insightful comments. We provide our responses to each specific issue in order.
Q1: I would suggest adding experiments on transformers if possible.
A1: **Intrusion detection and threat analysis is a computationally intensive task with stringent real-time requirements.**
Due to the complexity of attacks and their spatiotemporal persistence characteristics, it is necessary to detect large-scale provenance graphs.
We have try Transformers such as BERT and TinyBERT, due to the large dataset size (containing millions of unique system events), Transformers exhibited significantly higher processing times--as shown in Table 2, their event processing time is tens to hundreds of times that of traditional NLP models.
**Given the real-time requirements of the detection process, we abandoned some advanced models due to computational and time constraints.**
Referring to existing works, such as Flash [S&P'24], which uses Word2Vec for node encoding, and ProvDetector [NDSS'20], which employs Doc2Vec, we adopted similar NLP models and configurations, considering the need for efficient large-scale graph encoding.
Moreover, our experimental results (Table 4) indicate that the Transformer model fails to enhance detection performance in our task, primarily due to the unique characteristics of the provenance graph intrusion detection scenario. **While the Transformer architecture surpasses traditional NLP models in contextual modeling capability, the long-term and distributed nature of network attacks necessitates a broader analytical scope beyond a limited n-hop neighbors.**
In this context, simply applying SOTA models proves ineffective, leading to challenges regarding both effectiveness and scalability.
Q2: I would suggest the authors discuss more existing works on anomaly detection, e.g., CADE [USENIX'21].
A2: We have supplemented a table of experimental results comparing with SOTA approaches, highlighting its advantages in accuracy and the reduction of false alarms.
In the revised manuscript, since the detection granularity of our approach (path-level) differs from that of some SOTA works (graph-level or node-level), we have standardized the detection and comparison at the node level.
**The results demonstrate the advantages of our approach in terms of accuracy and the reduction of false positive.**
**Dataset: E3-CADETS**
||TPs|FNs|FPs|F1-score|
|-|-|-|-|-|
|Ours|32|1|69|0.4776|
|Nodoze|31|2|667|0.0885|
|ProvDetector|20|13|77|0.3636|
|Flash|7|25|6996|0.0019|
|Kairos|23|10|119878|0.0003|
**Dataset: E3-THEIA**
||TPs|FNs|FPs|F1-score|
|-|-|-|-|-|
|Ours|12|5|46|0.3200|
|Nodoze|12|5|105|0.1791|
|ProvDetector|0|17|91|0.0000|
|Flash|2|15|23330|0.0002|
|Kairos|11|6|10219|0.0021|
**Dataset: E3-TRACE**
||TPs|FNs|FPs|F1-score|
|-|-|-|-|-|
|Ours|17|1|1448|0.0229|
|Nodoze|17|1|2689|0.0125|
|ProvDetector|5|13|44|0.1493|
|Flash|4|14|60484|0.0001|
|Kairos|N/A|N/A|N/A|N/A|
Thank you for your thoughtful review, we will carefully refine our paper to ensure that its format, content, and presentation remain objective, accurate, and well-reasoned. | Summary: This paper proposes a learning-based anomaly detection method for provenance graphs, which are critical for cybersecurity. The approach decouples provenance graphs into system events, encodes them adaptively to handle out-of-vocabulary (OOV) elements and normality shifts, and trains lightweight regression models (MLP, LSTM, CNN) to predict event regularity scores. The experiment demonstrates high accuracy on DARPA datasets.
## update after rebuttal
Thanks for the authors' rebuttal. I have raised my score since most of my concerns have been addressed. However, I'm still concerned about some new results during the rebuttal, specifically, the usability considering the low F1-score (0.4776) and how you deal with your 69 false positives. I hope the authors can address them in the revised paper.
Claims And Evidence: Most of the claims are well-supported.
Methods And Evaluation Criteria: The methodology is clearly motivated by the challenges inherent in processing large-scale and dynamic provenance graphs. The authors explore multiple embedding models and regression models to determine the best combination for predicting event "regular scores" that indicate normal system behavior. The evaluation is performed on realistically simulated DARPA datasets, which is a conventional choice in this field. The authors use accuracy metrics, which are also standard for anomaly detection.
Theoretical Claims: The paper does not focus on deep theoretical derivations.
Experimental Designs Or Analyses: The paper reports detailed timing and accuracy metrics, which answers most of the research questions. I also like that the paper presents impressive ablation studies on embedding methods and OOV handling approaches.
However, it severely lacks comparison with other state-of-the-art provenance-based intrusion detection methods, such as those most related works the authors discuss. Besides, despite citing the scalability limitations of GNN-based methods, there have been more efficient GNNs (e.g., GAT, GraphSage), making it strange to exclude them arbitrarily from the comparison. In addition, the choice of $\alpha$ and detection thresholds is also not evaluated.
Supplementary Material: I have read the appendix, which contains the details of tag-propagation and additional results.
Relation To Broader Scientific Literature: The work builds on frequency-based anomaly detection (Hassan et al., 2019) and tag propagation (Li et al., 2024). It specifically addresses gaps in handling OOV elements and dynamic system behaviors, which are underexplored in prior PIDS literature.
Essential References Not Discussed: * GNN-based anomaly detection: The paper critiques GNNs’ computational overhead but omits comparisons with scalable GNN variants like GraphSAGE (Hamilton et al., 2017) or GAT (Veličković et al., 2018).
* Temporal graph learning: Methods like TGAT (Xu et al., 2020) could strengthen the handling of temporal information in provenance graphs (C3).
Other Strengths And Weaknesses: Strengths:
* The paper addresses a critical problem in real-time intrusion detection.
* The paper is well-written and well-structured; I enjoy reading it most of the time.
* It has a practical focus on real-time detection and storage efficiency, which is important to real-world use.
Weaknesses:
* Some parts of the paper would benefit from a clearer exposition, particularly regarding the selection and tuning of hyperparameters for the various embedding and regression models.
Other Comments Or Suggestions: Please refer to the questions below.
Questions For Authors: * Could the authors provide sufficient comparison experiments with other SOTA approaches?
* Why are GNN-based methods excluded from comparisons? Could they be used as baseline for evaluation?
* Could the authors elaborate on how the approach scales with increasing data rates and graph sizes in a production environment?
* How sensitive is the performance of your method to the choice of hyperparameters in the embedding and regression models and decay factor?
* Can the approach handle gradual shifts (not really unseen, but changing) in benign behaviors (e.g., software updates)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks for your review efforts and insightful comments. We provide responses to each specific issue.
Q1: GNN-based anomaly detection & Temporal graph learning
A1: GraphSAGE samples k-hop neighbors instead of traversing the entire graph. **APT attacks exhibit complex and prolonged spatiotemporal characteristics, requiring collecting a comprehensive provenance graph over an extended period for full capture**. Moreover, **provenance graphs are inherently complex, with multiple nodes and high average degrees, causing exponential information growth during propagation**.
GAT employs a global attention mechanism, making it more suitable for small graphs rather than large-scale provenance analysis. Our datasets are large: Cadets (309k entities, 5,509k events), Trace (505k entities, 910k events), and Theia (104k entities, 1,420k events). Cadets generates 2.6GB of audit logs daily over two weeks, while Theia spans 85GB in the same period.
Temporal graph learning models like TGAT or TGN encounter similar issues. While real-time detection is critical, **GNNs struggle with streaming data,** as time-windowed processing introduces latency. APT attacks spanning disjoint time windows further hinder GNNs from capturing the full attack chain.
Q2: The selection and tuning of hyperparameters for the various embedding and regression models
A2: We present the results of hyperparameter tuning for kernel regularizer. We observed similar patterns when tuning other hyperparameters like learning rates, loss functions and so on, finding that these hyperparameters had minimal impact on the model's regression performance. For embedding models, we used the default hyperparameters, adjusting only embedding dimensions, with results in Figure 3.
||Training Time(s)|Accuracy 1(%)|Accuracy 2(%)|
|-|-|-|-|
|L2(0.0001)|176.51|90.59|100.00|
|L2(0.001)|179.33|90.59|100.00|
|L2(0.01)|229.91|90.59|100.00|
|L1(0.0001)|174.01|90.59|100.00|
|L1(0.001)|278.39|90.59|100.00|
|L1(0.01)|123.69|35.86|0.00|
Q3: Sufficient comparison experiments with other SOTA approaches
A3: We provide a comparison table against SOTA approaches in the Cadets dataset, showing that our approach effectively reduces false positives and minimizes manual analysis efforts. We observe comparable results in the Theia and Trace datasets. In the revised manuscript, we standardize the different detection granularity to the node level.
||TPs|FNs|FPs|F1-score|
|-|-|-|-|-|
|Ours|32|1|69|0.4776|
|Nodoze|31|2|667|0.0885|
|ProvDetector|20|13|77|0.3636|
|Flash|7|25|6996|0.0019|
|Kairos|23|10|119878|0.0003|
Q4: Why are GNN-based methods excluded from comparisons? Could they be used as baseline for evaluation?
A4: In the preceding table, Flash utilizes GraphSAGE, while Kairos employs TGN. Flash reduces training overhead by limiting dataset size and graph traversal, while Kairos uses a time-window approach for real-time detection. Besides the delay introduced by collecting the first time window, **attacks may extend across multiple non-contiguous time windows, resulting in incomplete detection of the attack chain**.
Q5: How the approach scales with increasing data rates and graph sizes in a production environment?
A5: For real-time data streams, the model assigns a regular score immediately upon an event arrival, maximizing detection efficiency. The initial tags propagate and aggregate along graph edges as described in Section 3.2. **Memory usage grows linearly, and the required cache is minimal.** To prevent dependency explosions, we implement tag removal conditions to limit the number of cached tags, effectively controlling memory overhead.
Q6: How sensitive is the performance of your method to the choice of hyperparameters in the embedding and regression models and decay factor?
A6: The results for embedding dimensions are presented in Figure 3 (c&d). Q3 presents experiments on hyperparameter adjustments for regression models. We manually fine-tuned the decay factor to achieve the best detection results. As it is not a major contribution, further details are omitted from the main paper.
Q7: Can the approach handle gradual shifts in benign behaviors?
A7: **Our approach effectively adapts to gradual changes in benign behaviors.** Since gradual shifts may introduce OOV words that are not present in the training set, we encode them as zero vectors to ensure all anomalies are detected.
Benign nodes generally share more common elements with benign behaviors in the training set, whereas malicious nodes deviate more significantly from benign behavioral patterns.
**Since our unit of processing is an event, the regression model assigns benign-like regular scores to events with normal nodes and much lower scores to events related to malicious nodes.**
These regular scores serve as initial tags for the tag propagation algorithm, propagating and aggregating along edges to compute path-level regular scores. Alerts are triggered only for sequences of multiple suspicious events. | Summary: This paper proposes a novel learning-based anomaly detection method that effectively embeds and analyzes large-scale provenance graphs. The approach integrates dynamic graph processing with adaptive encoding mechanisms, which facilitates compact embeddings, effectively addresses out-of-vocabulary (OOV) elements, and adapts to normal variations in dynamic real-world environments. The enhanced baseline is incorporated into a label propagation framework to enable real-time detection. The main contributions are threefold: (1) An adaptive event encoding mechanism is designed to dynamically generate event vectors by analyzing frequency characteristics in system logs; (2) A lightweight regression model is developed to capture normal event distribution patterns with low computational overhead; (3) An integrated framework combining offline learning and online detection is established, where the offline phase constructs behavioral baselines while the online phase performs anomaly path detection through direct comparison with real-time data streams.
Claims And Evidence: This paper validates its claims through a comparative analysis of various embedding models in prediction tasks and anomaly path mining.
Methods And Evaluation Criteria: The proposed evaluation metrics – particularly prediction accuracy and precision/recall/F1-scores for fault detection – demonstrate practical significance for the addressed problem.
Theoretical Claims: The theoretical framework and mathematical formulations are fundamentally sound, offering valuable references for this research domain.However, the manuscript would benefit from explicit clarification of variable definitions in the equations, particularly regarding the specification of L and its operational semantics.
Experimental Designs Or Analyses: A comparative analysis of multiple embedding models in terms of performance is conducted, with a detailed examination of their respective advantages, disadvantages, and underlying reasons.
Supplementary Material: A review of previous contributions in this field is conducted, including the definitions of different embedding models as well as studies on network attacks and defenses.
Relation To Broader Scientific Literature: This paper provides a detailed review of previous contributions, highlighting their advantages and limitations. Based on the identified limitations, corresponding experiments are designed to address the existing issues.
Essential References Not Discussed: The selection of learning models does not include a discussion on Transformer or GRU.
It would be beneficial to discuss and compare more recent embedding models.
Other Strengths And Weaknesses: The experiments in the paper are comprehensive, with a strong emphasis on comparative studies. The proposed approach is tested on multiple models and datasets.
It effectively integrates graph networks with adaptive encoding, achieving compact embeddings of elements.
However, it does not include a comparative study with some of the latest neural networks or embedding models.
Other Comments Or Suggestions: There is a spelling error in the first paragraph of Section 3.2.
Certain definitions need to be clarified, such as the notation L in the text.
Additionally, the formulas for some embedding models should be properly introduced.
Questions For Authors: NA
Ethical Review Concerns: NA
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review efforts and insightful comments. We provide our responses to each specific issue in order.
Q1: The selection of learning models does not include a discussion on Transformer or GRU. It would be beneficial to discuss and compare more recent embedding models.
A1: **Intrusion detection and threat analysis is a computationally intensive task with stringent real-time requirements.**
Due to the complexity of attacks and their spatiotemporal persistence characteristics, it is necessary to detect large-scale provenance graphs.
We have try Transformers such as BERT and TinyBERT, due to the large dataset size (containing millions of unique system events), Transformers exhibited significantly higher processing times--as shown in Table 2, their event processing time is tens to hundreds of times that of traditional NLP models.
Given the real-time requirements of the detection process, we abandoned some advanced models due to computational and time constraints.
Moreover, our experimental results (Table 4) indicate that the Transformer model fails to enhance detection performance in our task, primarily due to the unique characteristics of the provenance graph intrusion detection scenario. While the Transformer architecture surpasses traditional NLP models in contextual modeling capability, **the long-term and distributed nature of network attacks necessitates a broader analytical scope beyond a limited n-hop neighbors.**
In this context, simply applying SOTA models proves ineffective, leading to challenges regarding both effectiveness and scalability.
Q2: It does not include a comparative study with some of the latest neural networks or embedding models.
A2: The rationale for not utilizing the latest embedding models aligns with our previous discussion.
**Given the unique characteristics of the provenance-based intrusion detection task and the prolonged, distributed nature of APT attacks, a broader graph structure must be collected and processed as contextual information.**
In this scenario, directly applying latest models often incurs substantial computational overhead, resulting in suboptimal efficiency and scalability.
Instead, we adopt a tag propagation algorithm, which efficiently aggregates contextual information with minimal storage for tags, thereby facilitating computationally efficient detection.
**As system logs accumulate over time, the provenance graphs inherently grow to a large scale.**
The Cadets dataset comprises 309k entities and 5,509k events, the Trace dataset include 505k entities and 910k events, and the Theia dataset contains 104k entities and 1,420k events. Specifically, the Cadets dataset spans approximately two weeks, generating 2.6GB of audit logs per day, whereas the Theia dataset, also covering two weeks, amounts to a total of 85GB. These figures underscore the substantial scale of provenance graphs.
Given the current state of technology, future analysis of log data from a single office computer may necessitate a high-performance server, posing significant challenges for real-world deployment.
GNN-based models or other latest neural networks primarily concentrate on small graphs or local n-hop neighbors.
However, **due to the prolonged spatiotemporal nature of attacks, attack chains typically span beyond the n-hop range.**
As a result, analyzing a larger graph structure becomes necessary, which increases the computational burden and leads to excessive resource consumption.
Some methods, such as Flash [S&P'24] and Kairos [S&P'24], have employed advanced neural network models, including GNN and TGN, respectively.
However, these models still face challenges in effectively solving the issues due to computational overhead.
They either reduce the training dataset or overlook critical graph information, which results in suboptimal training performance and poor detection outcomes.
Given these considerations, we did not employ the latest neural networks or embedding models for experiments, recognizing their inherent unsuitability for this task.
Q3: There is a spelling error in the first paragraph of Section 3.2. Certain definitions need to be clarified, such as the notation L in the text. Additionally, the formulas for some embedding models should be properly introduced.
A3: Thank you for your thoughtful review, we will carefully refine our paper to ensure that its format, content, and presentation remain objective, accurate, and well-reasoned. We will also add the necessary formulas to improve our paper. | Summary: The paper proposes a learning-based anomaly detection workflow for large-scale provenance graphs, addressing challenges like out-of-vocabulary elements and normality shifts in dynamic environments. It integrates dynamic graph processing with adaptive encoding to create compact embeddings, improving anomaly detection accuracy and adaptability. This approach is further enhanced with a tag-propagation framework for real-time anomaly path mining, significantly advancing provenance graph analysis for intrusion detection.
Claims And Evidence: The proposed model claims that they can handle real-time dynamic graph problem (OOV words) and they surely through some ways (treat them as all-zero vectors or Doc2Vec) to well solve it.
Methods And Evaluation Criteria: The experimental settings, including datasets and evaluation criteria, are fair. The method consists of existing works, but the workflows make sense.
Theoretical Claims: There’s no theoretical claim.
Experimental Designs Or Analyses: The experimental settings, including datasets and evaluation criteria, are fair.
Supplementary Material: I have reviewed all appendices of this paper.
Relation To Broader Scientific Literature: The contributions lie in the application perspective, all used modules come from existing works.
Essential References Not Discussed: The references covering contributions are comprehensive and well-explained.
Other Strengths And Weaknesses: **Strength:**
1) The paper is well-written.
2) The experimental settings are fair. The whole benchmark is relatively comprehensive.
3) The whole paper is well-organized and easy to follow.
**Weaknesses:**
1) The paper feels more like a benchmark for a new application scenario, with limited methodological innovation.
2) I wonder how many anomalous edges in the experiments are associated with OOV nodes. This may help to explain why treating OOV words as zero vectors significantly boosts detection performance. Could authors provide the ratio of anomalous nodes to normal nodes among all OOV nodes? Additionally, if the majority of OOV nodes exhibit normal behavior (in terms of edges), how would this affect performance?
3) I suggest renaming the Ablation Study section to Parameter Sensitivity, as Figure 3 doesn’t seem to effectively demonstrate an ablation study in this context.
Other Comments Or Suggestions: There are some inconsistent format errors, like the title of Appendix A.2.
Questions For Authors: Please refer to Weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your review efforts and insightful comments. We provide our responses to each specific issue in order.
Q1: The paper feels more like a benchmark for a new application scenario, with limited methodological innovation.
A1: This manuscript work towards to address an important and open research problem, namely, performing real-time provenance-based intrusion detection in an adaptive and scalable manner.
Specifically, the continuously generated audit logs in complex modern operating systems lead to the constant emergence of new entities and relationships, which causes out-of-vocabulary (OOV) problem. The presence of OOV words poses challenges to adaptability of the model. Furthermore, the complexity of attacks and their spatiotemporal persistence characteristics necessitate the detection of large-scale provenance graphs, leading to significant computational and memory overhead. **These challenges remain open problems in the field of cybersecurity, and existing works lack a general solution to address them.** In this paper, we propose an adaptive and scalability approach to reduce false positive and conduct efficient provenance-based intrusion detection.
Q2: How many anomalous edges in the experiments are associated with OOV nodes? Could authors provide the ratio of anomalous nodes to normal nodes among all OOV nodes? If the majority of OOV nodes exhibit normal behavior, how would this affect performance?
A2: We first refine the definition of OOV nodes mentioned in the comment. Each node may contain multiple words, and when a new node appears, it should be referred to as a node containing OOV words rather than simply an OOV node.
Anomalous edges fall into three categories:
(1) Both nodes are seen, but the edge represents an anomalous access;
(2) One of the nodes contains OOV words.
(3) Both nodes contain OOV words.
In the provenance graphs constructed from the *ta1-cadets-e3-official.json.1* log of the CADETS dataset, there are a total of 2,163,141 edges, among which 351 are anomalous.
Specifically, there are 2 edge of the first type, 30 edges of the second type, and 319 edges of the third type.
In the provenance graphs generated from the *ta1-cadets-e3-official.json.1* log of the CADETS dataset, there are a total of 114,969 nodes.
Among them, 2,372 nodes contain OOV words, accounting for 2.06% of all nodes.
Among these OOV-containing nodes, 833 are anomalous nodes, while 1,539 are normal nodes, with anomalous nodes comprising 35.11% of the total OOV-containing nodes.
Indeed, most OOV-containing nodes exhibit normal behavior. However, these nodes generally share more common elements with the training dataset, whereas malicious nodes deviate more significantly from the behavioral patterns in the training dataset.
**Since our unit of processing is an event (edge), the regression model assigns benign-like regular scores to events with normal nodes and much lower scores to event related to malicious nodes in most situations.**
During real-time detection, these regular scores serve as initial tags for the tag propagation algorithm, propagating and aggregating along information streams to compute path-level regular scores. Alerts are triggered only for sequences of multiple suspicious events.
Q3: I suggest renaming the Ablation Study section to Parameter Sensitivity.
A3: We agree that Figure 3 (a/b/c/d) addresses parameter sensitivity, but we believe that Figure 3 (d/f) demonstrates how our approach to processing provenance graphs significantly improves performance in terms of storage and computational resource compared to traditional frequency databases.
We provide a comparison table against SOTA approaches in the Cadets dataset, showing that our approach effectively reduces false positives and minimizes manual analysis efforts. We observe comparable results in the Theia and Trace datasets.
||TPs|FNs|FPs|F1-score|
|-|-|-|-|-|
|Ours|32|1|69|0.4776|
|Nodoze|31|2|667|0.0885|
|ProvDetector|20|13|77|0.3636|
|Flash|7|25|6996|0.0019|
|Kairos|23|10|119878|0.0003|
In the revised manuscript, since the detection granularity of our approach (path-level) differs from that of some SOTA works (graph-level or node-level), we have standardized the detection and comparison at the node level.
**The results demonstrate the advantages of our approach in terms of accuracy and the reduction of false positive.**
Nodoze [NDSS'2019] and ProvDetector [NDSS'2020] are based on frequency databases, and the results highlight that our approach to processing and embedding provenance graphs can improve detection performance compared to traditional methods.
Q4: There are some inconsistent format errors.
A4: Thank you for your thoughtful review, we will carefully refine our paper to ensure that its format, content, and presentation remain objective, accurate, and well-reasoned. | null | null | null | null | null | null |
DocKS-RAG: Optimizing Document-Level Relation Extraction through LLM-Enhanced Hybrid Prompt Tuning | Accept (poster) | Summary: The authors of the paper propose a novel approach for document-level relation extraction. During the training phase, they prepare two additional texts: one sourced from DocKG and the other from SetRAG, which are concatenated and utilized as a prefix in the final prompt. Subsequently, they fine-tune a small open-source language model to predict the relations present from the input document.
Claims And Evidence: Yes. The experiments conducted are on specific benchmark datasets; hence, the generalizability of the results to other domains or types of documents remains somewhat unspecified.
Methods And Evaluation Criteria: Yes. The selection of benchmark datasets specific to document-level relation extraction is appropriate. Both datasets are well-established in the field and are designed to evaluate models on complex, multi-entity document scenarios.
Theoretical Claims: Yes. The choice of using F1 and Ign-F1 scores as evaluation metrics is justified within the context of document-level RE tasks. The theoretical underpinning of why these metrics are particularly suitable for assessing the model's capabilities in capturing implicit relations could be discussed more rigorously.
Experimental Designs Or Analyses: Yes, the experiment design and analysis is suitable.
Supplementary Material: NA.
Relation To Broader Scientific Literature: Unlike traditional methods that often rely heavily on fine-tuning PLMs, the paper innovatively proposes a hybrid approach that enhances model adaptability by combining structural knowledge with contextual prompts, thus reflecting a significant evolution from earlier works that typically did not fully harness the potential of LLMs in this context.
Essential References Not Discussed: NA.
Other Strengths And Weaknesses: Strengths:
1)The paper is well-organized, with a clear delineation of the problem, proposed methodology, and experimental results.
2)The authors present their ideas logically, making it accessible for readers who may not have extensive background knowledge in document-level relation extraction.
Weaknesses:
1)The hybrid prompt generation process is complex and may be difficult for users unfamiliar with the underlying methodologies to interpret or adjust, which could limit its accessibility.
2)The emphasis on document-level relation extraction may not fully address the challenges posed by unstructured, noisy, or overly complex input data.
Other Comments Or Suggestions: 1)For further understandability, it would also makes sense to put some numbers in Figure 2 for each step e.g. GNN training which are then repeated in the corresponding section to guide the reader a bit more.
2)Although the paper provides a detailed methodology, some sections could benefit from greater clarity. For instance, the hybrid prompt generation process may require more concrete examples to fully illustrate the differences and advantages over conventional methods.
3)Could you provide a detailed explanation of the operations of Formula 10 and Formula 15?
Questions For Authors: 1)In your results, you mention challenges related to semantic misalignment between PLMs and knowledge graphs. Can you elaborate on how your framework specifically addresses this issue?
2)The authors propose a hybrid prompts generation method that combines structural interactions with semantic information. Could you clarify the process for generating these hybrid prompts, and perhaps provide examples of how they differ from standard prompts?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your valuable feedback.
C1: Although the paper provides a detailed methodology, some sections could benefit from greater clarity. For instance, the hybrid prompt generation process may require more concrete examples to fully illustrate the differences and advantages over conventional methods.
Response to C1: We appreciate your feedback, particularly regarding the clarity of the hybrid prompt generation process. We aim to enrich this section by including specific examples that illustrate how the generated prompts differ from those produced by conventional methods. By showcasing practical scenarios, we intend to clarify the advantages of our hybrid approach and its effectiveness in providing richer context for relation extraction tasks.
Q1: Could you provide a detailed explanation of the operations of Formula 10 and Formula 15?
Response to Q1: Thank you for your question. As illustrated in Section 4, the purpose of Formula 10 is to generate informative prompts based on the retrieved entities and relations from DocKG. It defines the prompt generation function $ g_{DocKG} $, which takes a set of relevant entities and relations as input and outputs structured prompts $ P_{DocKG} $. Formula 15 constructs hybrid prompts using the retrieved sentences from SetKB. It employs the generation function $ g_{SetRAG} $ to create prompts from the relevant triplets $ T_k $ while appending the retrieved sentences $ S_k $. This integration enriches the prompts by combining contextual insights with structured knowledge, enhancing the model's ability to perform document-level relation extraction accurately.
Q2: In your results, you mention challenges related to semantic misalignment between PLMs and knowledge graphs. Can you elaborate on how your framework specifically addresses this issue?
Response to Q2: Thank you for your thoughtful insights. As mentioned in Section 4.2, the embedding spaces of PLM and DocKG differ significantly. To address this issue, we integrate PLM embeddings as the initial inputs for entities and relations, which allows DocKG to learn from the PLM during the updating process and improves the reliability of similarity calculations.
Q3: Could you clarify the process for generating these hybrid prompts, and perhaps provide examples of how they differ from standard prompts?
Response to Q3: Thank you for your insightful feedback. As shown in Section 4.4, we incorporate both relevant structural and semantic information from DocKG and SetRAG. Specifically, we pre-defined various entity-relation mapping types. For example, if a subgraph has "Wisconsin" and "U.S." connected by the edge "state", it would be transformed into the statement "Wisconsin is a state of U.S." based on our mappings. Ultimately, we concatenate such statements with the relevant semantic information retrieved from SetRAG, and obtain the hybrid prompts. | Summary: In this paper, the authors propose a DocKS-RAG method to combine structural knowledge and semantic information for document-level relation extraction task. In DocKS-RAG, the authors first rely on GNNs to construct a document-Level knowledge graph and retrieve relevant information from this graph according to the user query. Then, they extract relevant sentences from the input document. On this basis, they construct hybrid prompts and adopt LORA to train an LLM. Extensive experiments on two datasets verify the effectiveness of the proposed method.
Claims And Evidence: The experiments on two widely-used benchmarks demonstrate the effectiveness of the method. Additionally, the ablation study shows the importance of each component in the method.
Methods And Evaluation Criteria: I believe that the proposed method is suitable for the problem. The motivation for combing structural knowledge and semantic information makes sense and is very important. As for knowledge construction, the proposed GNN-based method adopts a general pipeline in existing literature. As for semantic information, the extraction process is also acceptable. Additionally, the benchmarks and metrics are reasonable.
Theoretical Claims: This paper does not make any theoretical claims.
Experimental Designs Or Analyses: Yes, I have checked the details in Section 5, including the experimental setup and result analyses. The experiments in Section 5.5 verify the overall effectiveness and the influence of each hyper-parameter, while the results in Section 5.6 verify the importance of each module in the proposed method.
Supplementary Material: I have reviewed the whole supplementary material, including the benchmarks, baselines, and the implementation details.
Relation To Broader Scientific Literature: In my opinion, the proposed method provides a general perspective to address the issues of document-level RE task. The idea of integrating structural knowledge and semantical information is also general enough to extend to our domains or tasks.
Essential References Not Discussed: No
Other Strengths And Weaknesses: The main strengths of this paper include:
1. The motivation of combining structural knowledge and semantic information makes sense to me and is important.
2. The proposed method can effectively achieve the goal in this paper.
3. The experimental comparison with 14 baselines (including some SOTA methods) is solid and convincing.
The main weakness of this paper include:
1. Many technical details need to be further illustrated (please see the questions 3-5 below).
2. The technical contributions of this paper seem to be limited. The methods used to extract knowledge and relevant sentences in the document are very common in the literature. I don’t find essential improvements of the method.
3. The experimental section needs to be further revised (please see the question 6 below).
Other Comments Or Suggestions: There are some typos in this paper, such as:
1. Line 120, “model” should be “models”
2. Line 351, “a extra” should be “an extra”
Questions For Authors: 1. In Introduction, the authors state that “graph-based methods … lack of sufficient contextual information”. The authors need to explain why they believe graph-based methods lack contextual information and what specific types of context are missing.
2. Also in Introduction, the authors state that “PLMs are … the semantic misalignment between the texts and graphs”. I don’t understand how they address this issue in this paper.
3. In Section 4.2, the proposed method needs to train entity pair representations to construct the document-level knowledge graph. Where do the training samples come from? Besides, will this process limit the applicability of the method to other domains?
4. In Eq.(10), the authors introduce a generation function g_{DocKG}. How do they implement this function?
5. When explaining the extraction of knowledge graphs from the knowledge base, the authors mention the user query q. However, in Section 3 (Problem Definition), there is no indication that a user query is provided, and in Figure 1, the query is also not visible. The authors need to clarify this inconsistency.
6. In Section 5, the authors provide the hyper-parameter experiments before the ablation study, which seems to be weird for me. I suggest rearranging the order to improve clarity and coherence
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for recognizing and affirming our work. Regarding the questions raised during the review process, we have carefully considered them and provided detailed responses as follows:
Q1: In Introduction, the authors state that “graph-based methods … lack of sufficient contextual information”. The authors need to explain why they believe graph-based methods lack contextual information and what specific types of context are missing.
Response to Q1: Thank you for your valuable question. Graph-based methods primarily focus on the structural relationships between entities, which can obscure essential semantic nuances due to the static nature of graph representations. In complex document-level relation extraction tasks, entities may relate across texts, paragraphs, or even chapters within a document. This limitation in the graph-based approach restricts our understanding of how entities interact in different contexts, ultimately hindering the effectiveness of extraction.
Q2: Also in Introduction, the authors state that “PLMs are … the semantic misalignment between the texts and graphs”. I don’t understand how they address this issue in this paper.
Response to Q2: As shown in Section 4.4, we integrate informative structural knowledge from DocKG with the relevant sentences retrieved by SetRAG, and further generate the hybrid prompts to enhance the interaction between the textual data and the graph-based representations, thereby improving relation extraction performance.
Q3: Where do the training samples come from? Besides, will this process limit the applicability of the method to other domains?
Response to Q3: Thank you for your insightful questions. The training samples for constructing DocKG come from observable documentation data, which is utilized to obtain representations of entities and relations. In our proposed DocKS-RAG framework, the training process entails the construction of DocKG and SetKB. Relevant subgraphs and sentences are retrieved to create hybrid prompts, which are then fine-tuned using PEFT to improve the performance of LLMs in document-level relation extraction tasks. Although DocKS-RAG relies on this training process, it is adaptable and can be applied to other domains by fine-tuning the model with domain-specific data.
Q4: In Eq.(10), the authors introduce a generation function $ g_{DocKG} $. How do they implement this function?
Response to Q4: Thank you for your thoughtful insights. $ g_{DocKG} $ is implemented as a function for graph knowledge transformation. We pre-defined various entity-relation mapping types. For example, if a subgraph has "Wisconsin" and "U.S." connected by the edge "state", it would be transformed into the statement "Wisconsin is a state of U.S." based on our mappings. Ultimately, we concatenate such statements with the relevant semantic information retrieved from SetRAG, and obtain the hybrid prompts.
C1: When explaining the extraction of knowledge graphs from the knowledge base, the authors mention the user query q. However, in Section 3 (Problem Definition), there is no indication that a user query is provided, and in Figure 1, the query is also not visible. The authors need to clarify this inconsistency.
Response to C1: As mentioned in Section 4, q is denoted as the input user query for further extraction. We appreciate your insight and will consider including the explanations about q in the Problem Definition section and Figure 1 in the revised manuscript to enhance the readability.
C2: In Section 5, the authors provide the hyper-parameter experiments before the ablation study, which seems to be weird for me. I suggest rearranging the order to improve clarity and coherence.
Response to C2: Thank you for your valuable suggestion. We will consider making this change to the revised version. | Summary: In this work, the authors introduce DocKS-RAG, a framework that enhances large language models for document-level relation extraction. By integrating structural knowledge from a Document-level Knowledge Graph (DocKG) with semantic insights from a Sentence-level Semantic Retrieval-Augmented Generation (SetRAG) mechanism, the framework effectively captures complex relationships in documents. The paper emphasizes the importance of aligning structural and semantic knowledge to address the noise associated with traditional methods. Experiments on DocRED and Re-DocRED demonstrate that DocKS-RAG significantly improves accuracy and highlights the advantages of hybrid-prompt tuning techniques.
Claims And Evidence: The authors claim that their proposed framework, DocKS-RAG, addresses limitations in existing document-level relation extraction approaches by effectively combining linguistic and structural knowledge. Extensive experiments demonstrate that DocKS-RAG achieves superior performance metrics compared to state-of-the-art methods, as evidenced by significant gains in F1 and Ign-F1 scores. Additionally, the systematic ablation studies offered in the paper highlight the significance of each component, fostering confidence in the robustness of the framework's design and functionality.
Methods And Evaluation Criteria: In this paper, the authors use a Document-level Knowledge Graph (DocKG) alongside a Sentence-level Semantic Retrieval-Augmented Generation (SetRAG) mechanism, which allows the framework to capture both the structural relationships among entities and the contextual semantics of the text. This dual approach addresses the semantic misalignment typically observed between pre-trained language models and knowledge graphs, which is particularly crucial for complex document-level tasks.
Theoretical Claims: The paper asserts that employing a hybrid-prompt tuning approach, coupled with Parameter-Efficient Fine-Tuning (PEFT), leads to improved adaptability and performance of LLMs. This claim remains largely substantiated by experimentation.
Experimental Designs Or Analyses: An ablation study is conducted by removing different components of the DocKS-RAG framework, showing the impact of each component on performance. However, the nuances of the results could be better articulated—explaining why the removal of specific components leads to performance degradation would provide deeper insights into the framework's mechanics.
Supplementary Material: None.
Relation To Broader Scientific Literature: The study's emphasis on integrating structural knowledge via Document-level Knowledge Graphs (DocKG) echoes findings in the literature that suggest the synergy between PLMs and knowledge graphs (KGs) can improve contextual understanding. The approach taken in this paper thus not only aligns with but also advances previous investigations into the necessity of structural information in processing complex relationships within texts.
Essential References Not Discussed: The references are enough.
Other Strengths And Weaknesses: The idea of combining multiple retrieval and KG creation methods to form a RAG-based approach with heterogeneous data is interesting. The main novelty stems from the DocKG approach. The DocKG is generated by predicting if a relation should be added between two entities, given the embedding of the entities and the relation. The authors should ensure that all acronyms such as PLMs and KGs have been defined the first time they appear. This aids readers who may be unfamiliar with these terms.
Other Comments Or Suggestions: When mentioning the sentence-level Semantic Retrieval-Augmented Generation, it might be useful to briefly explain how it differs from typical retrieval mechanisms.
Questions For Authors: Although DocKS-RAG demonstrates high performance, the ablation studies indicate that competitive results can still be achieved without integrating structural and semantic components. For instance, simpler configurations that do not utilize DocKG or SetRAG yield reasonably good scores. Could the authors elaborate on the trade-offs between complexity and efficiency in practical deployments?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive feedback on our paper.
C1: When mentioning the sentence-level Semantic Retrieval-Augmented Generation, it might be useful to briefly explain how it differs from typical retrieval mechanisms.
Response to C1: Thank you for your valuable comment. Our proposed SetRAG module constructs a knowledge base from segmented sentences and retrieves contextually relevant information based on embeddings, allowing for improved understanding of the document's semantics. Such semantic information will be integrated with structural knowledge from DocKG, which further enhances the performance of LLMs in relation extraction tasks.
Q1: Although DocKS-RAG demonstrates high performance, the ablation studies indicate that competitive results can still be achieved without integrating structural and semantic components. For instance, simpler configurations that do not utilize DocKG or SetRAG yield reasonably good scores. Could the authors elaborate on the trade-offs between complexity and efficiency in practical deployments?
Response to Q1: Thank you for your thoughtful question. As shown in Table 4, the experimental results indicate that the integration of the DocKG and the SetRAG mechanisms significantly enhances model performance, demonstrating the effectiveness of our proposed DocKS-RAG module. In practical deployment scenarios, we capitalize on the parallelization capabilities offered by both DocKG and SetRAG, which allows for efficient processing without compromising the quality of relational extraction. Furthermore, by implementing strategies such as threshold retrieval, we manage to streamline the complexity of the operations involved. Integrating both modules enhances the model's adaptability to various document types and ensures robust performance in real-world applications. | Summary: The paper introduces DocKS-RAG, a novel framework aimed at enhancing document-level relation extraction (RE) by integrating large language models (LLMs) with structured knowledge graphs. The proposed method combines a Document-level Knowledge Graph (DocKG) with a Sentence-level Semantic Retrieval-Augmented Generation (SetRAG) mechanism to improve entity-relation understanding in complex documents. The authors conduct extensive experiments on benchmark datasets, DocRED and Re-DocRED, demonstrating that DocKS-RAG significantly outperforms existing PLM-based and graph-based methods by achieving superior F1 and Ign-F1 scores, thereby validating its effectiveness in addressing the intricacies of document-level RE tasks.
Claims And Evidence: The claims made in the submission regarding the efficacy and advantages of the DocKS-RAG framework in document-level relation extraction (RE) appear to be generally supported by clear and convincing evidence. The authors substantiate their claims through extensive experimental results, comparing their framework against existing state-of-the-art methods on benchmark datasets like DocRED and Re-DocRED.
Methods And Evaluation Criteria: Conducting ablation studies to evaluate the contribution of different components validates the efficacy of each aspect of the framework. This methodological rigor strengthens the argument for the importance of integrating both structural and contextual information in improving extraction performance.
Theoretical Claims: This paper primarily focuses on empirical methodologies rather than formal theoretical proofs. However, it does include theoretical claims regarding the effectiveness of the proposed methods, particularly the integration of structural knowledge and contextual understanding through the DocKS-RAG framework.
Experimental Designs Or Analyses: The authors compare DocKS-RAG against several established methods, including both PLMs-based and graph-based approaches. This comparative analysis is essential for establishing the framework's effectiveness.
Supplementary Material: The authors have made a commendable effort to enhance the reproducibility of their research by providing comprehensive access to both the code and the datasets used in their experiments. But I did not check the details of the provided code.
Relation To Broader Scientific Literature: Prior to this study, substantial efforts were made to enhance relation extraction primarily through sentence-level methods using pre-trained language models (PLMs), such as BERT (Devlin et al., 2019) and REBEL (Huguet Cabot & Navigli, 2021). The present paper's introduction of a document-level approach, specifically through the DocKS-RAG framework, builds on this prior work by addressing the limitations of existing PLMs-based methods, thus contributing to ongoing dialogues about enhancing RE capabilities.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
- The paper addresses a critical gap in natural language processing by focusing on document-level relation extraction, which is vital for tasks like knowledge graph construction and information retrieval.
- Extensive experiments on DocRED and Re-DocRED benchmarks are robust, showcasing superior performance in both F1 and Ign-F1 scores compared to state-of-the-art methods.
- Comprehensive ablation studies clarify the contributions of individual components (DocKG, SetRAG, and hybrid-prompt tuning), reinforcing the validity of the design choices.
Weakness:
- While the authors highlight the novelty of combining graph-based and LLM-based methods, the range of comparison baselines is limited. Existing works on the BioRED [1] dataset and similar benchmarks in knowledge extraction provide a richer set of methods that could offer additional insights into the framework’s relative performance. Incorporating these comparisons could strengthen the claim of novelty and demonstrate broader applicability.
- While DocKS-RAG achieves high performance, the ablation studies suggest that even without blending structural and semantic components, competitive results can be obtained. For example, simpler setups without DocKG or SetRAG achieve reasonably good scores. Could the authors elaborate on the trade-offs between complexity and efficiency in practical deployments?
Reference:
[1] Islamaj, Rezarta, et al. "The overview of the BioRED (Biomedical Relation Extraction Dataset) track at BioCreative VIII." Database 2024 (2024): baae069.
Other Comments Or Suggestions: Since the paper targets a broader audience, adding a small section that explains potential practical applications and user scenarios for the proposed framework could make the contributions more relatable. People appreciate understanding how theoretical advancements may impact real-world applications.
Questions For Authors: - In your discussion, you mentioned that existing graph-based methods can introduce noise and irrelevant connections, affecting performance. Can you elaborate on how DocKS-RAG specifically mitigates this noise during knowledge graph construction and retrieval processes?
- Regarding future work, how do you envision scaling DocKS-RAG to accommodate different types of documents or domains with vastly different structure or language use (e.g., legal texts, scientific literature)? What modifications might be necessary to adapt the framework effectively?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive comments and insightful questions.
Q1: While DocKS-RAG achieves high performance, the ablation studies suggest that even without blending structural and semantic components, competitive results can be obtained. For example, simpler setups without DocKG or SetRAG achieve reasonably good scores. Could the authors elaborate on the trade-offs between complexity and efficiency in practical deployments?
Response to Q1: We appreciate your insightful question. In practical applications, we take full advantage of the parallel processing capabilities provided by both DocKG and SetRAG, enabling us to handle tasks efficiently while maintaining high performance of relational extraction. Additionally, by applying threshold retrieval strategies, we could further simplify the complexity of our operations.
Q2: In your discussion, you mentioned that existing graph-based methods can introduce noise and irrelevant connections, affecting performance. Can you elaborate on how DocKS-RAG specifically mitigates this noise during knowledge graph construction and retrieval processes?
Response to Q2: Thank you for your valuable feedback. As presented in Section 4, firstly, DocKS-RAG applies a threshold parameter $ \tau_{er} $ during graph retrieval to filter out extraneous entities. Secondly, another threshold parameter $ \tau_{eq} $ is used to retrieve the relevant contextual sentences. Finally, DocKS-RAG generates hybrid prompts that combine the information from both the DocKG and SetRAG, which integrates relevant contextual information to enhance semantic alignment, improving the overall extraction performance.
Q3: Regarding future work, how do you envision scaling DocKS-RAG to accommodate different types of documents or domains with vastly different structure or language use (e.g., legal texts, scientific literature)? What modifications might be necessary to adapt the framework effectively?
Response to Q3: To scale DocKS-RAG for diverse document types or domains, modifications could include tailoring the DocKG construction to account for domain-specific terminology and relationships, alongside enhancing the SetRAG mechanism to accommodate varied syntactical structures and language use. Additionally, training additional domain-specific models or fine-tuning existing ones with targeted datasets would improve adaptability and semantic accuracy for specific contexts. | null | null | null | null | null | null |
Make LoRA Great Again: Boosting LoRA with Adaptive Singular Values and Mixture-of-Experts Optimization Alignment | Accept (poster) | Summary: The paper proposes the GOAT, an SVD-derived LoRA-MoE finetuning framework. Through SVD decomposition, the authors found that existing LoRA finetuning schemes are insufficient due to restrictive training on only specific pre-selected SVD segments. Based on this finding, the authors proposed employing a LoRA-MoE architecture for finetuning, initializing each LoRA expert with different SVD segments and dynamically selecting segments via MoE during training. To enforce alignment of GOAT with full finetuning, specialized optimization for weight and gradient alignments are designed. Based on experiment results against various baselines on different datasets (tasks), GOAT is demonstrated to yield superior performance in almost all cases.
Claims And Evidence: Yes. The paper claims that:
1) the integration of SVD segments via dynamic selection is necessary to achieve good initialization for LoRA(-MoE) finetuning;
2) specialized optimization for alignment to full finetuning is necessary to improve model performance.
These claims are supported by:
- good preliminary empirical analysis in Fig. 1, which shows the effects of initializing different SVD segments for different scenarios;
- good method design demonstrating the integration of SVD segments into LoRA-MoE architecture and the computation of W_res and s for weight and gradient alignment;
- good experiment performance showing SOTA performance.
Thus, the claims made within the paper are well supported.
Methods And Evaluation Criteria: Yes.
The proposed method is sensible.
- Employing MoE to facilitate dynamic selection of LoRA related to specific SVD segment is a reasonable design.
- The mathematics for deriving W_res and s for alignment appears sensible.
The benchmark datasets are sensible.
- Since GOAT is task-agnostic, both vision and language tasks are used in the experiment.
- The baseline (compared) algorithms are recent, with most published in 2024.
Thus the overall methods and evaluation are sensible.
Theoretical Claims: Yes. The critical mathematical proofs in paper are predominantly focused on finetuning alignment (Section 3.3). They are found in Appendix C. Specifically:
- Lemma 3.1-3.4 appears correct, and are generally intuitive.
- (Minor Weakness) Lemma 3.5 requires (non-intuitive) knowledge about Leaky-ReLU with negative slope of sqrt(5) resulting in Var(A)=1/(3n). Please cite the source or provide additional proof for this information.
Aside from the minor clarification required at Lemma 3.5, the critical proofs appear correct.
Experimental Designs Or Analyses: Yes. The experiment designs are considered valid.
- A good variety of image and language tasks are considered, with GOAT outperforming baseline methods in most cases.
- The ablation study, as shown in Table 5, compares GOAT with alternative schemes of initialization on only the principal, minor, and random to validate the claim that SVD-based initialization is necessary.
- Table 7, when taken together with Table 1 and Table 3, shows that GOAT does not introduce excessive parameters, and utilizes similar GPU RAM and training time compared to baseline methods. This demonstrates that the experiment evaluates GOAT against baseline methods fairly.
- (Minor Weakness) For Fig. 7, is load balancing used during training? While load balancing is necessary for most MoE training, it also weakens the conclusion of "validates on the effectiveness of each SVD chunk". This is because balanced workload distribution is enforced by the load balancing loss, rather than implicitly achieved through SVD-based initialization alone.
Aside from minor clarification required from Fig. 7, the experiment and analysis design are valid.
Supplementary Material: Yes. The supplementary material contains the code for execution (also provided as an anonymous git). The provided README is sufficiently detailed to conduct code execution for reproduction if necessary.
Relation To Broader Scientific Literature: - The research advances ongoing research on improving the performance of LoRA-finetuned models. The paper focuses particularly on addressing deficiencies in parameter initialization. GOAT outperforms existing initialization techniques, such as PiSSA and KaSA. GOAT also introduces another perspective on weight alignment wrt full finetuning orthogonal to preceding works, such as DoRA and analysis by (Shuttleworth, 2024).
- The integration of LoRA with Mixture-of-Experts expands on an emergent trend of Mixture-of-LoRA frameworks, such as MoLE (Wu, 2024) and MixLoRA (Li, 2024). Moreover, the author provides SVD-based analyses to justify the use of Mixture-of-LoRA frameworks to ameliorate low-rank-related deficiencies found in conventional LoRA finetuning.
References:
Shuttleworth, R., Andreas, J., Torralba, A., & Sharma, P. (2024). Lora vs full fine-tuning: An illusion of equivalence. arXiv preprint arXiv:2410.21228.
Wu, X., Huang, S., & Wei, F. (2024). Mixture of lora experts. arXiv preprint arXiv:2404.13628.
Li, D., Ma, Y., Wang, N., Ye, Z., Cheng, Z., Tang, Y., ... & Tang, M. (2024). Mixlora: Enhancing large language models fine-tuning with lora-based mixture of experts. arXiv preprint arXiv:2404.15159.
PiSSA, KaSA, and DoRA are cited within the reviewed paper.
Essential References Not Discussed: No. To the knowledge of this reviewer, no essential references are missing.
Other Strengths And Weaknesses: The authors have investigated an important problem (improving LoRA-finetuning) and proposed an interesting design with solid analyses and good experiment results. However, some additional weaknesses are noted below.
Weakness (not previously addressed):
- (Weakness) The goal of Section 2.2 (Rethinking Scaling Factor) is not understood. What is the final verdict from the exploration? Specifically, how does this exploration relate to alignment wrt full-finetuning?
- (Minor Weakness) The pseudocode of your algorithm should be presented (if necessary, in the appendix).
- (Minor Weakness) On Figure 3.II, please emphasize that the goal is to find W_res and s. Currently, this is not intuitive without scrutiny over the figure (font too small for W_res and s) and explicit rereading of Section 3.3 (please set the closed-form solutions for W_res and s as labelled equations).
Other Comments Or Suggestions: None.
Questions For Authors: For ease of reference, these comments/questions regarding weaknesses in the paper are repeated below. Upon providing satisfactory response, the overall recommendation will be changed to Accept (from Weak Accept).
1) (Minor Weakness, More Information) Lemma 3.5 requires (non-intuitive) knowledge about Leaky-ReLU with negative slope of sqrt(5) resulting in Var(A)=1/(3n). Please cite the source or provide additional proof for this information.
2) (Minor Weakness, Clarify) For Fig. 7, is load balancing used during training? While load balancing is necessary for most MoE training, it also weakens the conclusion of "validates on the effectiveness of each SVD chunk". This is because balanced workload distribution is enforced by the load balancing loss, rather than implicitly achieved through SVD-based initialization alone.
3) (Weakness, Revision) The goal of Section 2.2 (Rethinking Scaling Factor) is not understood. What is the final verdict from the exploration? Specifically, how does this exploration relate to alignment wrt full-finetuning?
4) (Minor Weakness, More Information) The pseudocode of your algorithm should be presented (if necessary, in the appendix).
5) (Minor Weakness, Revision) On Figure 3.II, please emphasize that the goal is to find W_res and s. Currently, this is not intuitive without scrutiny over the figure (font too small for W_res and s) and explicit rereading of Section 3.3 (please set the closed-form solutions for W_res and s as labelled equations).
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: # Response to Reviewer `4qHz`
> Q1: Lemma 3.5 requires (non-intuitive) knowledge about Leaky-ReLU with negative slope of sqrt(5) resulting in Var(A)=1/(3n). Please cite the source or provide additional proof for this information.
>
Thanks for your suggestion. We follow the derivation of the commonly used Kaiming initialization[1] (assuming activation function is Leaky ReLU[2]):
Proof: Leaky ReLU is defined as $f(x)=x \text{ if } x \geq 0, \text{else } f(x) = a·x (a = \sqrt{5})$
Following Kaiming initialization[1], assume input $x$ is zero-mean with variance $\sigma^2$, symmetrically distributed ($P(x \geq 0) = P(x < 0) = \frac{1}{2}$),
we can obtain output variance as:
$$Var(f(x)) = \frac{1}{2}(1 + a^2)\sigma^2=3\sigma^2 \quad (a^2 = 5)$$
To ensure unit variance per layer ($Var(y)=1$), because $Var(y) = n Var(x)$, where $n$ is the layer width (fan-in).
$n Var(f(x)) = 1 \implies 3n\sigma^2 = 1 \implies \sigma^2 = \frac{1}{3n}$,
Thus, weights $A$ should be initialized with $Var(A) = \frac{1}{3n}$.
[1] Delving Deep into Rectifiers: Surpassing Human-Level Performance on ImageNet Classification (ICCV2015)
[2] Empirical Evaluation of Rectified Activations in Convolution Network (2015)
> Q2:For Fig. 7, is load balancing used during training? While load balancing is necessary for most MoE training, it also weakens the conclusion of "validates on the effectiveness of each SVD chunk". This is because balanced workload distribution is enforced by the load balancing loss, rather than implicitly achieved through SVD-based initialization alone.
>
Thank you for raising this insightful point. In Fig.7, we use load balancing, but the conclusion holds because:
- Section 2.1 shows single-LoRA initialization via distinct SVD segments (no load balancing), the Fig.1 revealing their dataset-dependent roles.
- We further ablate the load-balancing in GOAT (2in8, Cars task), which confirms all experts remain active (see table below), proving each SVD chunk contributes meaningfully.
|GOAT|f1|f2|f3|f4|f5|f6|f7|f8|
|-|-|-|-|-|-|-|-|-|
|w/o loadbalance|0.1043|0.1379|0.1275|0.1094|0.1207|0.1405|0.1259|0.1338|
> Q3: The goal of Section 2.2 (Rethinking Scaling Factor) is not understood. What is the final verdict from the exploration? how does this exploration relate to alignment wrt full-finetuning?
>
The goal of Section 2.2 is to establish two key insights: (1) Weight initalization alignment alone is insufficient - gradient alignment is equally crucial (2) The scaling factor s fundamentally controls gradient dynamics.
Section 2.2 experiments (Figure 2) reveal that even with perfect initalization alignment, common choices (s=2) produce small gradient norms and slow convergence. Increasing s - particularly in low-rank settings - boosts gradient magnitudes and accelerates training. This leads to Lemma 2.2: scaling factor s directly governs gradient behavior, meaning poor s choices degrade optimization dynamics regardless of weight initialization.
This motivates our core contribution in Theorem 3.2 and Theorem 3.5. Theorem 3.2 establishes that both weight initialization and gradient updates must align for $W_{LoRA}$ to track $W_{FFT}$ based on the first insight. In Theorem 3.5, we chose to derive the optimal s to ensure gradient updates alignment, as the second insight and experiment tells us control s is a practical way to adjust the gradient dynamics. Together, these theorems provide a complete framework where proper scaling factor selection enables LoRA to match full fine-tuning performance through principled optimization dynamics.
> Q4: The algorithm pseudocode should be presented.
>
Thank you for your reminder. We incorporate the following pseudocode in the revised paper:
Algorithm: GOAT
Input: $x$ (input),$n$ (input dim), $\eta, \rho$ (hyperparameter), $E$ (num experts)
- Set Scaling Factor: $s = \sqrt{\frac{3n\eta}{r}}$
- SVD Decomposition: $W_0 = U \Sigma V^\top$
- Initialization ($\forall i \in [1,E]$):
- trainable component: $B_0^i = \sqrt{\frac{1}{s\rho}} U' \Sigma'^{1/2}, \quad A_0^i = \sqrt{\frac{1}{s\rho}} \Sigma'^{1/2} V'^\top$
- residual component: $W_{\text{res}}^+ = \frac{s}{E} \sum_{i=1}^E B^i_0 A^i_0, \quad \tilde{W_0} = W_0 - W_{\text{res}}^+$
- Forward ($\forall i \in [1,E]$):
- Compute gating weights: $w^i(x)$
- Output: $\tilde{W_0}(x) + \sum_{i=1}^E w^i(x) s B^i_0 A^i_0(x)$
> (Q5) On Figure 3.II, please emphasize that the goal is to find W_res and s. Currently, this is not intuitive without scrutiny over the figure (font too small for W_res and s) and explicit rereading of Section 3.3 (please set the closed-form solutions for W_res and s as labelled equations).
>
Thanks for your valuable advice. We will revise our figure to make it clearer. | Summary: This paper proposed a PEFT method with SVD-structured MoE and theoretical scaling. It initializes LoRA MoE experts with distinct singular value segments, and derives an optimal weight alignment strategy and scaling scheme to improve both convergence speed and performance. Extensive experiments on 25 tasks validates the effectiveness of the proposed method.
Claims And Evidence: Most of the claims are supported, but there are still a few claims that are not convincing to me:
(1) In Theorem 3.1, the authors claim that ‘we can align LoRA with Full FT’, ‘addresses the performance gap in single LoRA architectures’. Actually, the proposed method is still worse than full finetuning in most of the tasks, as shown in the experiments. In my opinion, this proposed method can only reduce the gap between LoRA and full FT, so the contribution here should be clarified.
(2) In Theorem 3.5, the authors derive the optimal scaling factor from an assumption: there is a fixed learning rate ratio between full tuning vs. LoRA. However, as the learning rate (LR) is actually a hyperparameter, we cannot know the optimal LR for finetuning before we really do multiple runs of full FT, which is not applicable in PEFT setting. If the LR for full FT is arbitrarily selected in practice, the derived scaling value looks less useful. Moreover, in real experiments, we usually use a LR scheduler, and the LR ratio between LoRA and FT are even changing along the training trajectory, posing additional challenges for this assumption.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No.
Experimental Designs Or Analyses: Yes, all of those in the experiments section.
Supplementary Material: No.
Relation To Broader Scientific Literature: The initialization of weights and scaling methods are novel.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The paper could be improved for better clarity. For example, there is no algorithm description for the whole method, so the whole algorithm is splitted into different sections which hinders the readability.
Other Comments Or Suggestions: Typo: L195 ‘segement’, Figure 3 ‘Graident Alignment’.
Questions For Authors: No.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Response to Reviewer `5G79`
> Q1:In Theorem 3.1, the authors claim that ‘we can align LoRA with Full FT’, ‘addresses the performance gap in single LoRA architectures’. Actually, the proposed method is still worse than full finetuning in most of the tasks, as shown in the experiments. In my opinion, this proposed method can only reduce the gap between LoRA and full FT, so the contribution here should be clarified.
>
Thanks for your suggestion. Due to practical limitations (e.g., low-rank approximation, error accumulation), which may impact theoretical alignment, we will address this in the revision.
> Q2:
In Theorem 3.5, the authors derive the optimal scaling factor from an assumption: there is a fixed learning rate ratio between full tuning vs. LoRA. However, as the learning rate (LR) is actually a hyperparameter, we cannot know the optimal LR for finetuning before we really do multiple runs of full FT, which is not applicable in PEFT setting. If the LR for full FT is arbitrarily selected in practice, the derived scaling value looks less useful.
Moreover, in real experiments, we usually use a LR scheduler, and the LR ratio between LoRA and FT are even changing along the training trajectory, posing additional challenges for this assumption
>
Thanks for your insightful question. To clarify, the learning rate ratio in our framework serves as a tunable hyperparameter, not a fixed constant. This means in practice, rather than arbitrarily selecting a full FT learning rate by multiple exhaustive full FT runs, one can first identify an optimal LR specifically for LoRA (which is computationally more feasible), then tune the ratio hyperparameter to implicitly define the corresponding optimal LR for full FT. In fact, similar assumptions and approaches have been validated and utilized effectively in existing literature [1]
Regarding dynamic LR scheduling, it does not impact the alignment. This is because our theoretical framework is grounded on aligning the weight updates: $\eta_{\text{FFT}} \cdot g_{\text{FFT}} = \eta_{\text{LoRA}} \cdot g_{\text{LoRA}}$. i.e. $\frac{\eta_{\text{LoRA}}}{\eta_{\text{FFT}}} g_{\text{LoRA}} \approx g_{\text{FFT}}$, as long as LoRA and full FT share identical learning rate scheduling patterns at each training iteration, the relative LR ratio $\frac{\eta_{\text{LoRA}}}{\eta_{\text{FFT}}}$ remains consistent.
To empirically substantiate this theoretical robustness, we refer readers to **Table 6**, where we report results across various LR settings. Our approach consistently maintains superior performance, exceeding baseline methods by a clear margin of 1.09-2.56 points, demonstrating its practical resilience and broad applicability.
[1] LoRA-GA: Low-Rank Adaptation with Gradient Approximation (NeurIPS2024)
> Q3:The paper could be improved for better clarity. For example, there is no algorithm description for the whole method, so the whole algorithm is splitted into different sections which hinders the readability.
>
Thank you for your reminder. We incorporate the following pseudocode in the revised paper:
Algorithm: GOAT
Input: $x$ (input),$n$ (input dim), $\eta, \rho$ (hyperparameter), $E$ (num experts)
- Set Scaling Factor: $s = \sqrt{\frac{3n\eta}{r}}$
- SVD Decomposition: $W_0 = U \Sigma V^\top$
- Initialization ($\forall i \in [1,E]$):
- trainable component: $B_0^i = \sqrt{\frac{1}{s\rho}} U' \Sigma'^{1/2}, \quad A_0^i = \sqrt{\frac{1}{s\rho}} \Sigma'^{1/2} V'^\top$
- residual component: $W_{\text{res}}^+ = \frac{s}{E} \sum_{i=1}^E B^i_0 A^i_0, \quad \tilde{W_0} = W_0 - W_{\text{res}}^+$
- Forward ($\forall i \in [1,E]$):
- Compute gating weights: $w^i(x)$
- Output: $\tilde{W_0}(x) + \sum_{i=1}^E w^i(x) s B^i_0 A^i_0(x)$
> Q4:Typo: L195 ‘segement’, Figure 3 ‘Graident Alignment’.
>
Thanks for your valuable advice. We will carefully revise our paper based on your suggestions. | Summary: This paper presents GOAT (Great LoRA Mixture-of-Experts), a novel framework to enhance the LoRA MoE structure for fine-tuning LLMs. GOAT (1) adaptively initializes each expert using different SVD segments to integrate relevant priors from pre-trained models, and (2) derives a theoretical scaling factor that aligns LoRA MoE optimization with Full FT by minimizing gradient misalignment. Experiments across 4 multi-task benchmarks demonstrate GOAT’s superior performance than existing LoRA MoE-based methods, closing the gap with Full FT.
Claims And Evidence: Why does the scaling scheme for gradient alignment with Full FT theoretically improve performance? In other words, the gradient update of Full FT may not always be optimal across all scenarios, as it is influenced by factors such as training data and learning rate. Therefore, aligning with Full FT does not necessarily guarantee the best results.
Moreover, the GOAT+ method in Appendix D, which achieves a more precise alignment with Full FT, appears to perform slightly worse than the GOAT method. This raises concerns about whether strict alignment is indeed beneficial in practice.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: Yes, the paper provides correct theoretical derivations to support the claims.
Experimental Designs Or Analyses: 1. Could you provide detailed settings and selection strategies for the coefficient of the load balancing loss used in GOAT and other MoE-based methods? Since this coefficient can significantly impact the final performance, a clearer explanation would be beneficial.
2. Given that GOAT improves convergence speed, is it fair to train all methods for the same carefully selected number of epochs detailed in Appendix E.5? Would it be more appropriate to compare the best performance achieved by each method instead?
Supplementary Material: Yes.
Relation To Broader Scientific Literature: Somewhat.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: No.
Other Comments Or Suggestions: No.
Questions For Authors: No.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Response to Reviewer `9dgB`
> Q1: Why does gradient alignment with Full FT improve performance theoretically, given that Full FT's updates aren't always optimal due to data/learning rate dependencies?
>
Thanks for your insightful question. First, Full FT outperforms LoRA in most cases, making it a natural alignment target in previous works [1].
Second, For scenarios where Full FT perform poorly, is because that its unregularized fitting capacity in low-data regimes lead to overfitting on intricate patterns and noise in smaller datasets. (e.g., CoLA, MRPC with 8.5K and 3.6K samples only in Table 4)
In contrast, our method combines Full FT strengths with three key regularizers to mitigate overfitting issues:
- Low-Rank Updates: low-rank updates enforce robust feature learning and reduce sensitivity to noise [2].
- MoE Architecture: Experts specialize in distinct patterns, avoiding over-adaptation to spurious variations.
- SVD initalization: Experts are initialized by different pretrained SVD-segmented features, enhancing specialization and mitigating overfitting.
Thus, our method approximates Full FT’s strong fitting ability while avoiding its pitfalls, achieving comparable or superior performance (e.g., CoLA in Tables 4).
[1] LoRA-GA: Low-Rank Adaptation with Gradient Approximation (NeurIPS2024)
[2] LoRA Learns Less and Forgets Less (TMLR2024)
> Q2: Does the slightly worse performance of GOAT+ in Appendix D, despite its more precise alignment with Full FT, suggest that strict alignment may not be beneficial in practice?
>
Sorry for the confusion. GOAT+ is not intended as an improvement over GOAT (not a more precise alignment), but rather as a variant that explores a different assumption.
In GOAT, we assign the same scaling factor to each expert, even though each expert is initialized with a different singular value, leading to varying norms. In contrast, GOAT+ adjusts each expert’s scaling factor in proportion to its singular value, ensuring that the product of the scaling factor and singular value is consistent across all experts. While this adjustment doesn't always improve performance, we found the underlying assumption interesting enough to include it in our appendix.
In the ablation study (Table 5), removing the module responsible for aligning with Full FT degrades performance, demonstrating the effectiveness of strict alignment. We will revise the naming in the paper to avoid any confusion.
> Q3:Could you provide detailed settings and selection strategies for the coefficient of the load balancing loss used in GOAT and other MoE-based methods?
>
Thanks for your suggestion. We use top-k routing with k=2 and set the coefficient for the balance loss to 1e-3.
We attach the load-balancing loss coefficient experiment by activating 2 out of 8 experts on Cars.
|coefficient|GOAT|MoLoRA|HydraLoRA|
|-|-|-|-|
|1e-1|49.09|49.02|48.45|
|1e-2|50.52|49.33|**49.45**|
|1e-3|**53.50**|**50.83**|48.42|
|1e-4|51.53|49.03|48.52|
|0|49.85|48.02|49.06|
We can observe that setting the coefficient too low (e.g., 0 or 1e-4) leads to expert imbalances, which in turn degrades performance. Conversely, excessively high coefficients (e.g., 0.01 or 0.1) can disrupt the normal learning process. Our results show that a coefficient of 1e-3 achieves the best tradeoff in GOAT/MoLoRA between balancing expert load and maintaining stable learning.
Notably, GOAT consistently outperforms across all tested coefficients, demonstrating its robustness in these settings.
> Q4: Given GOAT's faster convergence, is it fair to train all methods for the same number of epochs (Appendix E.5)? Should we compare the best performance of each method instead?
>
To clarify, our evaluation strategy indeed follows your suggestion by comparing the best performance achieved by each method. Specifically, we train each model for a sufficiently large number of epochs so that the loss converges to a stable plateau, then evaluate the model at every epoch and select the best-performing result for all baselines.
For the epoch number:
- NLG/NLU: We use more epochs than previous studies to ensure convergence. For example, while prior work often uses just one epoch for NLG tasks [1,2], we employ five epochs to guarantee convergence.
- Commonsense Reasoning: We strictly follow prior work [3] by using a large dataset (approximately 170K samples) to ensure thorough convergence. We then directly compare our results with the best-reported values from earlier studies, where our method still achieves superior performance.
- CV: we retain the original epoch settings from previous work [4], as they ensure proper convergence for each task.
[1] KaSA: Knowledge-Aware Singular-Value Adaptation of Large Language Models (ICLR2025) (ICLR2025)
[2] LoRA-GA: Low-Rank Adaptation with Gradient Approximation (NeurIPS2024)
[3] DoRA: Weight-Decomposed Low-Rank Adaptation (ICML2024)
[4] Localizing Task Information for Improved Model Merging and Compression (ICML 2024) | Summary: The paper proposes a novel fine-tuning framework for LoRA (Low-Rank Adaptation) MoE (Mixture-of-Experts). Two challenges identified in the paper: 1) how to design an effective initialization for the matrices A and B across different experts. 2) unaligned optimization leads to large gradient gap and slow convergence rate.
Accordingly, the paper first proposes initializing LoRA MoE experts with distinct singular value segments, allowing the router to select the appropriate prior information. It then derives an optimal weight alignment strategy and a theoretical scaling scheme to improve gradient alignment.
Extensive experiments on 25 tasks demonstrate that the method's superiority while maintaining scalability. Compared with Full fine-tuning, the proposed method shows comparable or even better performance.
### update after rebuttal
My concerns about experiment evaluations are mostly addressed. Thus, I remain positive about this paper.
Claims And Evidence: The claims are mostly supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed method and evaluation criteria are well-aligned with the problem. A better LoRA initialization method is crucial for narrowing the performance gap between parameter-efficient tuning and full fine-tuning. It is commendable that the proposed approach is validated on extensive CV and NLP tasks.
Theoretical Claims: Yes, I have checked the theorems in Section 3.3. Theoretical Optimization Alignment, both the initialization and gradient alignment. The claims seem reasonable.
Experimental Designs Or Analyses: I have checked the experiment part. The performance evluation metrics are not clear in Table 1-4.
Supplementary Material: I have checked C. Proof of Theoretical Results.
Relation To Broader Scientific Literature: The intialization of AB matrices in LoRA is a rising topic and has been studied in previous methods, including PISSA [1] (tuning the principal components) and MiLoRA [2] (tuning minor singular components). For LoRA-MoE, the initialization has not been well studied, the proposed method divides the SVD of W into different segments and allocate segments to different experts. From this perspective, the proposed method is a timely study.
[1] PiSSA: Principal Singular Values and Singular Vectors Adaptation of Large Language Models
[2] Milora (MiLoRA): Harnessing Minor Singular Components for Parameter-Efficient LLM Finetuning
Essential References Not Discussed: NA
Other Strengths And Weaknesses: Strengths：
1. The motivation is clear. Relying solely on either the principal or minor singular values is not ideal and does not guarantee optimal performance across different datasets. In LoRA MoE, different experts can be responsible for different parts of the task. Moreover, the effects of the scaling factor are also crucial for optimization
2. Evaluations are quite comprehensive. Significant Improvement over othe LoRA MoE methods, and in NLP benchmarks the proposed method is even better than Full FT. The proposed method also shows good scalability across different rank and different expert numbers.
Weakness:
1. The routing strategy in the proposed method is not clear. In Formula (12), it introduces a soft routing stratey, while in Figure 6, it shows the results of different activation ratio. A more clear description and analysis of the MoE router’s behavior would provide valuable insights, particularly in terms of its latency, and potential routing biases.
2. The paper does not adequately introduce the practical applications of LoRA MoE, nor does it sufficiently demonstrate the real-world impact of the proposed method.
3. To my knowledge, existing approaches typically train multiple LoRA experts for different tasks. However, this paper does not report results on multi-domain datasets, especially in Image classification and NLU tasks, which limits its practical relevance.
Other Comments Or Suggestions: It would be better to incoporate the practical importance of LoRA MoE in the introduction by highlighting its real-world applications, like multi-task or multi-domain scenarios.
Questions For Authors: 1. In table 1, the single LoRA method comparison part, methods like PiSSA and MiLoRA achieves worse performance than LoRA. Are there any analysis on this phenomenon?
2. Do you experiment with alternative routing techniques in LoRA MoE? Could you discuss how these different strategies impact performance?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Response to Reviewer `ETXs`
> Q1: The performance evaluation metrics are unclear.
>
Sorry for the confusion. Here is a more detailed explanation of our performance metrics:
- NLU & CV: Accuracy, except for CoLA (Matthew’s correlation). See Appendix E.1 for details.
- CommonSense: Exact match.
- NLG: GSM8k(Exact match), Human-Eval(Pass@) and mtbench: (First-turn score (GPT-4))
We will incorporate these clarifications into our revised version of the paper.
> Q2: Clearer description and analysis of the MoE router’s strategy and behavior, especially regarding latency and potential biases, would be valuable.
>
To clarify, we use a top-k routing strategy (Eq(10) and (12)), where each token selects the top k experts based on the highest router logits.
We offer insights about topk hyperparameter, routing biases and latency in Figure 6, 7, and Table 7:
- **Top‑k Hyperparameter:** Figure 6 shows performance vs. the k/E (E is total number of experts) activation ratio in top-k routing. Activating 2 out of 8 experts balances sparsity and performance, so we use this setting in Tables 1–4.
- **Routing Biases and Load Balance**: Figure 7 shows token distribution across experts. CV and NLU tasks exhibit balanced expert usage, while NLG tasks favor the first two experts, suggesting larger SVD chunks play a key role in complex generation, aligning with PiSSA’s insights.
- **Latency:** Section 4.9 (Computation Analysis) and Appendix F.1 provide a detailed breakdown of latency and computational efficiency.
> Q3: The paper lacks an adequate introduction to the practical applications and real-world impact of LoRA MoE.
>
Thanks for your advice. We will incorporate additional discussion on the practical applications and real-world impact of LoRA MoE into the revised version of the paper.
MoE is popular for managing large parameters while activating only a sparse subset during inference, making it ideal for large-scale models. However, in Section 4.9 and Table 7, without optimization, fully fine-tuning an MoE model significantly increases trainable parameters and FLOPs compared to Full FT.
LoRA MoE addresses these challenges by replacing experts with low-rank matrices, reducing computation, preserving MoE benefits, and enabling faster training, lower memory usage, and reduced energy consumption—crucial for resource-limited or real-time applications.
For instance, in NLP, where large-scale models are common, LoRA MoE achieves SOTA performance with lower computational cost. This efficiency benefits industries like autonomous driving, healthcare[1], where lower latency and costs enhance performance and scalability.
Overall, LoRA MoE balances MoE's model capacity with cost-effective deployment, making it adaptable to various real-world applications.
[1]Hydralora: An asymmetric lora architecture for efficient fine-tuning(NeurIPS2024)
> Q4:This paper doesn’t report results on multi-domain datasets.
>
We actually conducted experiments on Commonsense using a multi-domain setting. In Table 3, our evaluation method for commonsense reasoning follows a classic multi-domain setting, following prior work[1]. We train on a 170K multi-task mixed dataset and evaluate on **8 datasets**. Our approach outperforms the single LoRA method by at least 1.2 points and the LoRA MoE method by at least 1.6 points.
[1] DoRA: Weight-Decomposed Low-Rank Adaptation(ICML2024)
> Q5:An analysis of why PiSSA and MiLoRA perform worse than LoRA in Table 1.
>
To clarify, previous works[1,2] show that PiSSA and MiLoRA don't always outperform LoRA. KaSA found that PiSSA accelerates convergence but uses limited pre-trained knowledge at lower ranks, limiting performance. Similarly, MiLoRA’s minimal adjustments to pre-trained weights often fail to improve over LoRA. In Table 1, we adopt the same rank settings as KaSA and reach the same conclusion.
In contrast, our method consistently achieves superior performance across both low and high ranks by effectively balancing convergence speed and final performance, as demonstrated in Tables 1–4 and Figure 5.
[1]MiLoRA: Harnessing Minor Singular Components for Parameter-Efficient LLM Finetuning (NAACL2025)
[2]KaSA: Knowledge-Aware Singular-Value Adaptation of Large Language Models (ICLR2025)
> Q6. Do you explore alternative routing techniques in LoRA MoE, and how do they affect performance?
>
Thanks for your suggestion. In our paper, we use the commonly adopted top-k routing and set k=2 based on the analysis in Figure 6. we primarily adopt top‑k routing. We extend our experiments to include alternative routing strategies such as top-p routing and a top‑k variant with shared experts below.
| Routing Strategy | avg. ACC |
| --- | --- |
| **Ours(top-k=2)** | **81.30** |
| top-p(0.25) | 79.40 |
| top-k + share expert | 78.68 |
We find that, compared to other approaches, setting k=2 achieves the best performance.We will incorporate these into our revised version of the paper. | null | null | null | null | null | null |
Stochastic Poisson Surface Reconstruction with One Solve using Geometric Gaussian Processes | Accept (poster) | Summary: The paper improves the stochastic Poisson surface reconstruction [25], which combines the interpolation and surface reconstruction into a single stage. The method avoids the complicated finite element method and makes use of Fourier transformation. It also proposes to use Monte Carlo samples from the posterior to reduce memory cost. The paper also presents several applications, e.g., collision detection and ray-casting.
## update after rebuttal
I appreciate that the authors' rebuttal addressed some of my concerns. I maintain my score, which is positive for the paper.
Claims And Evidence: Fourier domain analysis relies on periodic kernel functions and boundary conditions, but actual point cloud data are often non-periodic. Does this assumption limit the practical applicability of the methods?
"one can view both the vector field and implicit surface as functions on the torus". Why torus? Is there any topology constraint? Can the method deal with high genus models?
Methods And Evaluation Criteria: The evaluation criteria in the current work are rather simplistic, and as a result, they do not provide sufficient support for effectively assessing the methods in question. I suggest to design more evaluations and compare with [25] comprehensively, including, accuracy, scalable etc.
Theoretical Claims: The paper proposed complex theories for stochastic Poisson reconstruction. During Amortized cross-covariance, $f_{k,v}$ is pre-computed on a grid and simple linear interpolation is applied to evaluate $f_{k,v}$. Does the grid occupy too much space? What is the resolution?
Experimental Designs Or Analyses: The paper improves the time and space efficiencies of the original SPSR [25]. The experiments should valid the time and space on large point cloud comprehensively. However, only a few examples are demonstrated. The numbers of points are not presented. Since approximations are used during Gaussian process, the quantitative accuracies are expected in the experiments. Currently, the evaluations cannot support the claims very well.
Supplementary Material: I reviewed the Section B in the supplementary.
Relation To Broader Scientific Literature: This is a very theoretical paper that uses the Gaussian process for Poisson surface reconstruction. I am not sure about the practical applicability.
Essential References Not Discussed: N.A
Other Strengths And Weaknesses: N.A.
Other Comments Or Suggestions: N.A.
Questions For Authors: When Monte Carlo sampling is used to reduce memory consumption, how is the representativeness of the sampling results to the posterior distribution ensured? Is there statistical bias due to insufficient sampling times?
It is possible to generalize the the method to screened Poisson surface reconstruction?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you very much for your review! Let us address your points below:
> "Fourier domain analysis … limit the practical applicability of the methods?”
> “Why torus? Is there any topology constraint?”
In short: **no, it does not limit applicability**. This is because the periodic boundary conditions needed to leverage our Fourier methods apply to the **bounding box inside of which the point cloud sits, not to the point cloud or reconstructed surface** - the point cloud and surface do not need to be periodic in any way.
More specifically, to avoid periodic boundary conditions affecting reconstruction, we situate the point cloud sufficiently-far from the boundary to limit their effect: **this mirrors what is done in ordinary PSR**, which imposes other types of boundary conditions (say, Dirichlet or Neumann), and moves the point cloud far-enough away from the boundary so that it is largely unaffected by them.
From a mathematical standpoint, the main reason for using periodic boundary conditions - and, therefore, the torus - is because (a) its Fourier analysis is much simpler compared to alternatives and (b) it works. One could instead try to develop a method using, say, properties of the sphere, but this would necessitate computations in terms of spherical harmonics, which are more complicated than the sines and cosines we use. We therefore think extensions like this are better left to future work.
> “The evaluation criteria in the current work are rather simplistic … I suggest to design more evaluations and compare with [25] comprehensively, including, accuracy, scalable etc”
> “Since approximations are used during Gaussian process, the quantitative accuracies are expected in the experiments.”
We agree that improved evaluations would strengthen the paper (though with the caveat that we have followed the SPSR baseline paper’s lead and focused on qualitative evaluations because they are important in graphics applications), and to this end have **completed a number of additional evaluations looking at things like the effect of hyperparameters** on results, and timing experiments. We are additionally **aiming to add a quantitative next-view planning comparison** to the final manuscript draft. We describe these additional experiments to be added to the appendix - both the ones that are complete with results, and those still in progress - in detail in our response to Reviewer vrrd.
> “Does the grid occupy too much space? What is the resolution?”
We use a grid of size $50^d$. As all of the experiments are done for $d = 3$, the grid size is ~500 KB of memory. More broadly, we agree with the importance of comprehensively evaluating how grid size affects performance, and have performed **additional experiments showing a too-small amortization grid results in over-smoothing**, which we will add to next manuscript version’s appendix.
> “The experiments should valid the time and space on large point cloud comprehensively”
This is a good idea: **we have added an experiment, which uses points sampled from the Stanford Dragon mesh, and examines runtime**: we find that using 64 points takes a 15 seconds (much of it we suspect due to Python overhead), 4096 points takes about 30 seconds, and using 65536 points takes about 5 minutes. We will add a plot showing this to the next manuscript version.
> “When Monte Carlo sampling is used to reduce memory consumption, how is the representativeness of the sampling results to the posterior distribution ensured? Is there statistical bias due to insufficient sampling times?”
Since our posterior is a Gaussian process, we can use direct Monte Carlo sampling, which is by definition unbiased (as opposed to, say, other settings which require Markov chain Monte Carlo methods or similar). However, one might be concerned about variance of posterior functionals: here, it is a good question to ask how many samples are enough in practice, as is requested by Reviewer vrrd.
To address this, we will add **additional comparisons which show how transmittance calculations and collision detection performance varies with the number of Monte Carlo samples** to the next manuscript draft.
> “It is possible to generalize the the method to screened Poisson surface reconstruction”
This is an interesting question! It seems highly plausible that an extension of our approach would work, but it would require analytically re-computing the relationship between the Karhunen-Loeve decompositions, which would be sufficiently-involved mathematically that we believe it is best to defer it to future work.
---
# Summary
Overall, your suggestions have led us to **improve the writing** - in particular, to emphasize that our Fourier formulation does not restrict the kinds of surfaces we can reconstruct - as well as the **strength of evaluations** used for this work. On behalf of these additions, we would gently like to ask whether you would consider increasing your score.
---
Rebuttal Comment 1.1:
Comment: I appreciate that the rebuttal makes the work clearer. I choose to keep my positive evaluation. | Summary: The paper uses techniques from geometry Gaussian process to speed up the stochastic Poisson surface reconstruction method.
## Update after rebuttal
I appreciate the authors' efforts in providing a more nuanced discussion and additional comprehensive results. Given this, I keep my score which is already positive.
Claims And Evidence: I'm not convinced by the claim that the proposed method qualitatively matches the outputs of SPSR in Section 4.1. In the first paragraph, the authors support this claim by comparing Figures 1 and 3 in this paper with Figure 11 in the SPSR paper. However, these comparisons are performed on different objects which cannot be directly compared. Since it is straightforward to generate results on the same object using identical slices, I expect a side-by-side comparison with SPSR on the same objects (including mean, variance, and probability).
Methods And Evaluation Criteria: Despite the paper’s contribution to accelerating SPSR, supported by both theoretical analysis and quantitative results, it lacks qualitative comparisons with SPSR. In contrast, SPSR provides extensive qualitative comparisons with PSR, as seen in Figures 1, 3, 7, 8, 18, and 20. These comparisons are crucial, as the contribution of speeding up SPSR is diminished if the method does not maintain the original reconstruction quality. I elaborate more on this in other sections.
Theoretical Claims: The theoretical claims look good to me.
Experimental Designs Or Analyses: I'm convinced by the theoretical analysis and results demonstrating the improvement in terms of the speed over SPSR, despite that, there are some limitations:
1. A key contribution of the paper is replacing the computation of means and covariances with Monte Carlo sampling from the posterior, avoiding the need to store posterior covariances. However, the paper lacks discussion on how the number of Monte Carlo samples impacts both reconstruction speed and quality.
2. A more fair qualitative comparison with SPSR is necessary to justify the quality claims, as mentioned in my comments under Claims and Evidence.
Supplementary Material: I reviewed the proof part and appendix C.
Relation To Broader Scientific Literature: The proposed method has the potential for broad applicability in accelerating various tasks, including surface reconstruction and ray casting in computer graphics, as well as collision detection in autonomous driving and human-robot interaction.
Essential References Not Discussed: To the best of my knowledge the essential related works are cited.
Other Strengths And Weaknesses: Overall, I acknowledge the paper's contribution to the community as a sped-up version of SPSR, with the local querying capabilities and mathematically principled approach.
Other Comments Or Suggestions: -
Questions For Authors: I would appreciate it if the authors could provide a more in-depth discussion on Monte Carlo sampling, particularly its impact on reconstruction speed and quality. Additionally, a more comprehensive qualitative comparison with SPSR would help better support the claims made in the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review! We appreciate that you mentioned our method **“has the potential for broad applicability”** and that we have a **“mathematically principled approach”** which was indeed part of our motivation for this work.
> “I'm not convinced by the claim that the proposed method qualitatively matches the outputs of SPSR in Section 4.1”
> “Despite the paper’s contribution to accelerating SPSR… diminished if the method does not maintain the original reconstruction quality”
These are very good points: but addressing them involves some nuance. First, let us **draw attention to the following distinction between tasks** (also mentioned in our response to Reviewer otmx):
1. **“Surface reconstruction”**: given a point cloud, produce a reconstructed surface
2. **“Uncertainty quantification for surface reconstruction”**: given an underlying surface reconstruction algorithm, and noisy or otherwise imperfect inputs, produce an estimate of uncertainty for the reconstructed surface
From this viewpoint, **our proposed algorithm’s purpose is 2 - that is, uncertainty quantification for surface reconstruction**, where the “underlying surface reconstruction algorithm” is classical PSR (or more precisely, a minor variant thereof, given our slightly-different boundary conditions).
With this framing, we **agree improved evaluations would strengthen** our paper, but where the **focus should be on stochastic aspects to do with uncertainty** as opposed to the mean reconstructed surface, which is essentially the same as in classical methods. Mirroring the standard in graphics and in the SPSR paper (our baseline), our focus has been on qualitative properties, though we agree quantitative evaluations would strengthen our paper further. To this end, we have decided to add additional experiments to the next manuscript’s draft in the form of an expanded appendix:
1. This includes a **comprehensive examination of how hyperparameters affect results**: we find that (a) too-small an amortization grid density leads to over-smoothing, (b) SGD and Cholesky perform similarly (assuming the latter succeeds), (c) for sufficiently-small length scales, the SPSR baseline can result in over-smoothing, whereas our approach works well.
2. We have also **performed runtime comparisons**, which show our approach to be faster than SPSR as long the length scale is not too large (note that the small length scale regime is the interesting one, as this allows the algorithm to capture fine surface details).
3. We are additionally working on a **quantitative evaluation examining how the produced uncertainty affects next-view planning**, as a way to test how our algorithm’s numerics affect situations where one needs to use the produced uncertainty for a downstream purpose.
We hope that these additions - of which the first two are complete - will help strengthen our evaluations and therefore alleviate your concerns.
> “A key contribution of the paper is replacing the computation of means and covariances with Monte Carlo sampling from the posterior.”
> “I would appreciate it if the authors could provide a more in-depth discussion on Monte Carlo sampling”
Thank you for raising these points: due to their importance, let us respond in two parts.
First, in situations where this is viable, we utilize analytic expressions derived from eqn. (6) to compute means and covariances rather than sampling: in hindsight, this point came out somewhat-hidden in our text, as we wanted to emphasize sampling as a new capability compared to baselines. We will therefore **modify the next draft to make this clearer** - thank you for drawing our attention here!
Second, in situations where sampling is needed, we agree that further evaluation of the number of Monte Carlo samples needed is appropriate. Since the random functions we are sampling do come from Gaussian process posteriors, we expect the number of samples needed, in most cases, to be similar to other situations where Gaussian process sample paths are used - such questions are explored to some degree in the pathwise conditioning papers, though for different purposes. To address this, we will add **additional comparisons which show how transmittance calculations and collision detection performance varies with the number of Monte Carlo samples** to the next manuscript draft.
---
# Summary
Overall, your suggestions have led us to **significant improvements, both in terms clarity and especially the evaluations we present**, which we believe, based on those parts we were able to complete so far, will significantly strengthen our results. On behalf of these additions, we would gently like to ask whether you would consider increasing your score.
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. I appreciate the authors' efforts in providing a more nuanced discussion and additional comprehensive results. Given this, I keep my score which is already positive. | Summary: Poisson surface reconstruction (Khazdan et al.) is the task of fitting a function $v(x)$ to point cloud data $(x_i, v_i)_i$ and solving $\Delta f = \nabla \cdot v$ for $f$ (subject to, e.g., Neumann boundary conditions). Then, the zero-level set of $f$ is the desired surface.
Stochastic poisson surface reconstruction (SPSR; Sellan and Jacobsen) proceeds similarly but models $v$ as a Gaussian process (GP), which makes $f \mid v$ a GP with tractable mean and covariance. But this is costly because (loosely speaking) point clouds contain many points, and because solving PDEs is expensive.
The submission proposes ways to make stochastic Poisson surface reconstruction more efficient by using geometric Gaussian processes, pathwise conditioning, and SGD-based Gaussian process training.
The paper proposes a set of refinements to make SPSR more efficient. These refinements focus on leveraging geometric Gaussian processes, pathwise conditioning, and efficient linear solvers. Specifically, the contributions include:
- Make $v$ a Gaussian process that automatically satisfies the boundary condition of the PDE. Choosing a periodic boundary implies Matern processes on the $d$-dimensional Torus do precisely that. Such processes admit known Karhunen-Loeve expansions (Borovitskiy et al.).
- Deduce a Karhunen-Loeve expansion for $f$ from $v$ and $\Delta f = \nabla \cdot v$. This is possible because operations like $\nabla$ and $\Delta$ can be computed in closed form for the Fourier-like terms in the expansions for $v$.
- Avoid working with conditional covariance matrices, and only ever sample from the posterior via pathwise conditioning (Wilson et al.), implementing joint samples from $p(f, v)$ and the cross-covariance between $f$ and $v$ via the expansions. The cross-covariance is expensive to evaluate, so an amortisation scheme is proposed. This avoids an explicit (typically, FEM-based) Poisson solve. What remains in terms of linear algebra is that pathwise conditioning requires solving a linear system involving a Gram matrix.
- To solve this linear system, the submission uses Lin et al.'s SGD-based algorithm instead of, for example, inducing points.
Claims And Evidence: The submission makes the following claims (using the formulations from the paper's conclusion):
- **A single linear solve (for interpolation), as opposed to two linear solves in SPSR (one for interpolation, one for PDE solving).** This is accurate, even though the manipulation of Fourier coefficients of $f$ and $v$ could be regarded as something like a linear solve, too. (Appendix B suggests that one million summands are used for representing the cross-covariance, so evaluating the terms sounds relatively expensive, too.) But from a linear algebra perspective, there is no explicit PDE solver.
- **The computational cost of the proposed method depends on where the solver is queried, not the size of finite element meshes.** This is also accurate, even though it disregards the computational complexity of interpolation via pathwise conditioning, which solves a linear system that involves a Gram matrix with as many rows and columns as the point cloud has data points. However, this cost is the same for both SPSR and the proposal, so it's fair to ignore it.
- **The same set of statistical queries as in prior work are supported.** This is more or less accurate, because even though the queries are available, they all rely on evaluating densities, means, or standard deviations based on samples from the Gaussian, which leads to approximations. Prior work evaluates them exactly, but based on a model of reduced complexity (diagonal covariances). Qualitative results suggest that queries can be evaluated reasonably well by using samples, but there are no quantitative results (more on quantitative results in "Methods and Evaluation Criteria"). Further, I could not find information on how many samples are used for generating the queries in Figures 1 and 3, which means there are some open questions.
- **A first step in incorporating sample-efficient data acquisition schemes.** There is a mention of this point in Section 3, but no concrete suggestion and no (theoretical or empirical) evidence is provided. This seems to be more future work than a contribution (which is fair, as there is a page limit), but since both the abstract and the introduction also mention it, perhaps these claims could be weakened. For reference, the main prior work (Sellan and Jacobsen) proposes and benchmarks one such scheme (Sellan and Jacobsen, Figure 15).
In evaluating the claims, I find that the submission provides strong qualitative evidence but could benefit from additional quantitative analysis.
Overall, I think the submission's claims are supported relatively well by evidence, and even though qualitative results would make the improvements more convincing, I think this is a nice paper, and I lean towards recommending acceptance.
I discuss the lack of quantitative evidence under "Methods and Evaluation Criteria" below.
Methods And Evaluation Criteria: I appreciate the Figure's focus on readability and on visually explaining the similarities and differences between existing SPSR and the proposal. I like the numerous qualitative results. That said, the submission would be stronger with quantitative results. The absence of quantitative analysis is why I only give a borderline score.
More specifically, the experiments discuss the following scenarios:
1. **Figures 1 and 3** show that the mean and standard deviation of the samples yield "good-looking" results. However, there is no mention of quantitative results, like calibration metrics, or at least ratios of standard deviation and mean error. It's also unclear how the reconstruction reacts to changing $L$ (or any of the other hyperparameters) beyond one sentence in the caption of Figure 3. Is there a way of taking an exactly known shape (a sphere?), generating a point cloud, and seeing how the reconstruction error is affected by parameters like $L$ or the number of data points?
2. **Figure 2** shows how the proposed algorithm can resolve small lengthscales because it's not limited by the memory demands of a finite element mesh. It's a bit unclear what ``lengthscale'' means here. According to Section 1, it's a hyperparameter of the prior over $v$. But in Figure 2, it seems to be an (induced?) hyperparameter for $f$. I think I understand the high-level point in Figure 2, but if possible, some more precision in the terminology for "lengthscale" would be nice. And since we're talking about hyperparameters of Gaussian process models, does the proposed algorithm offer a mechanism to calibrate hyperparameters, e.g. via marginal likelihoods? And again, if there were some more quantitative error analysis, the point of SPSR not capturing these points would be more convincing than looking at a single example.
3. **Figure 10** demonstrates that the algorithm's runtime scales with the number of query points, not the number of FEM points. This is all under the assumption that $L$ is fixed (and sufficiently large), using the amortisation from Section 3.3, and that the term $K^{-1} (\mathbf{v} - v(x))$ has been computed, correct? I am asking, because precomputing all $L$ terms and amortising the covariance feels like there is a corresponding performance gain in the FEM solver to be explored (something along the lines of precomputing the inverse of the matrix and amortising that result). I like the result in Figure 10, but perhaps there is some nuance to provide in the analysis. Or have I misunderstood something?
4. Another criticism is that the proposed algorithm contains multiple new components that are only benchmarked on surface reconstruction in combination, never on their own. Currently, it seems that the combination of approaches works well; however, for example, the combination of pathwise conditioning and SGD-based solves seems to be applicable to the baseline SPSR algorithm, too, with perhaps notable performance improvements. Same (but maybe to a lesser extent) for geometric Gaussian processes. To be fair, the paper only claims that the combination is helpful, but it would be nice to see that using either component isn't enough.
In summary, I like the demonstrations. But I think the submission would gain clarity with (some of) the following investigations:
- Investigating the role of $L$ on the reconstruction quality (on a toy example, if necessary).
- Investigating the number of samples needed for reasonable results in statistical queries. With these kinds of results, I think the submission would be strengthened
- A more quantitative version of Figure 10 (eg a "No. points queried" vs "Runtime" plot) that more clearly shows the linear complexity gain.
Ideally, there would also be independent benchmark studies for the different components. Mainly, to demonstrate whether it's the combination of geometric GPs and pathwise conditioning with SGD that leads to the good performance, or whether either of those two components suffices. That said, I understand it's a big ask, so I'm okay with this change not happening (even though I'd like to see it).
Theoretical Claims: I have checked the proofs of Propositions 1 and 2 in Appendix A. I appreciate the thorough derivation.
However, Equation (11) could benefit from more clarification.
Beyond Propositions 1 and 2, all theoretical claims are known.
Experimental Designs Or Analyses: Covered by "Methods and evaluation criteria" above.
Supplementary Material: I reviewed the full supplement.
Relation To Broader Scientific Literature: The paper extends prior work on stochastic Poisson surface reconstruction (SPSR) with a number of computational considerations. Most of these techniques are known (and cited in the paper):
- Geometric Gaussian processes
- Pathwise conditioning
- SGD-style linear-system solving
The combination of these techniques and the derivation of the Karhunen-Loeve expansion of $f$ based on that of $v$ are new, to the best of my knowledge. As such, I think the submission embeds well into related work, but also provides a series of new results.
Essential References Not Discussed: All essential references are discussed.
Other Strengths And Weaknesses: See the other sections.
Other Comments Or Suggestions: - It might help readability if the term "formal" is used more consistently. In the sentence after Equation (5), it means "rigorous". In Appendix A, it means "non-rigorous".
- It might also help readability if the term "problem-(in)dependent" is replaced by something more accurate. For example, Section 3.3 says that $k_{f, v}$ is problem-independent" which means that $k_{f, v}$ is independent of the point cloud (i.e. the surface being constructed). There are many subproblems in this algorithm (interpolation, Fourier coefficients respectively, PDE solving, amortisation, sampling, etc.), and I got confused by "problem-dependent" regularly. But this is my subjective opinion, and my recommendation doesn't depend on this change.
Questions For Authors: - The proposed algorithm seems to be much faster than previous approaches to stochastic Poisson surface reconstruction. How close is it (in runtime and memory demands) to non-stochastic Poisson surface reconstruction?
- Figure 3 mentions diminishing results beyond $L=20^3$, and Appendix B mentions that the experiments use $L=100^3$. The latter is unexpected, given the former. Where does this discrepancy come from?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review! We are very happy that you recognized our approach as **“more efficient”** than prior ones and that our **“claims are supported relatively well by evidence.”** We address your questions below:
> “manipulation of Fourier coefficients … something like a linear solve.”
> “Appendix B suggests … relatively expensive”
This is a fair point - but let us add a critical distinction: **our Fourier coefficients depend only on the kernel and not on the point cloud,** unlike the linear solves in SPSR. This property enables amortization, so one can precompute Fourier-coefficient manipulations once in advance, rather than on a per-point-cloud basis.
> “how many samples … generating the queries in Figures 1 and 3”
These are done using analytic expressions derived from eqn. (6) rather than sampling: in hindsight, this point came out somewhat-hidden in our text, as we wanted to emphasize sampling as a new capability compared to baselines. We will modify the next draft to improve this.
> “A first step in incorporating … one such scheme (Sellan and Jacobsen, Figure 15).”
We largely agree, with one tiny exception: **we do introduce a modified score function in Sec. 3.4**, which can be evaluated much faster than the one from the original SPSR paper, but is otherwise similar. Due to space constraints, we cut this in favor of future work: for completeness, we will **add a comparison between the two in the appendix of the next draft**, following the setup presented in Figure 15 of "Neural Stochastic Screened Poisson Reconstruction", Sellán and Jacobson, SIGGRAPH Asia 2023 (which studies the more-general screened Poisson surface reconstruction setting), and will modify our claims as you suggest.
> “could benefit from additional quantitative analysis”
We acknowledge that our results are less-quantitative than many ML works: this is similar to prior work such as SPSR, and reflects norms in the graphics community. We nonetheless agree quantitative evals would strengthen the work, and will add a number of such comparisons to the appendix, described in further detail in our response to Reviewer vrrd.
> “…unclear how the reconstruction reacts to changing $L$ … Figure 3”
> “…role of $L$ on the reconstruction quality”
Thank you for this idea. We’ve done some preliminary tests, and **found that setting $L$ too small results in loss of high-frequency details**. The same holds for using too-coarse a grid for amortization. We will add this to the next draft’s appendix.
> “Figure 2 shows … (induced?) hyperparameter for “f”.”
In both cases, **this is a hyperparameter**, specifically the number $\kappa$ distances are scaled by before going into the kernel, $k(x,x') = k(\frac{x-x'}{\kappa})$, which determines both $v$ and in turn $f$. We will make this clearer.
> “… mechanism to calibrate hyperparameters … more convincing”
This is an excellent question. Since our kernel-matrix solve is identical to that of an ordinary GP, one way to do this would be to apply **standard maximum marginal likelihood techniques**. We will add discussion on this.
> “Figure 10 … number of query points … Or have I misunderstood something?”
You are correct that $L$ is fixed and sufficiently large (we use $L = 100^3$ as mentioned in Appendix B). Here, allow us to again emphasize that our cross-covariance is independent of the input point cloud. While one may be able to optimize FEM meshes for specific point clouds, **we can compute our cross covariance once and reuse it for any point cloud.**
> “Another criticism is that the proposed… either component isn't enough” and “Independent benchmark studies”
This is a good idea. We ran additional comparisons on the difference between SGD and Cholesky factorization, which **show that performance (provided Cholesky works) is comparable**, and will add them to the appendix. In the case of pathwise conditioning, we mainly view this as new functionality, since SPSR’s global nature limits the attainable resolution of samples.
> “A more quantitative version… linear complexity gain”
Good idea! We will add this to the next draft’s appendix.
> “Equation (11) .. clarification”
Here, $P(x \in \Omega) = P(f(x) \leq 0)$ as our implicit surface representation takes on negative values inside $\Omega$, zero on the boundary of $\Omega$, and positive values outside of $\Omega$. We will make this more clear in the camera ready.
> “term "formal" .. consistently”
> “term "problem-(in)dependent"
Thank you for these - we will fix them.
> “How close is it … to non-stochastic [PSR]?”
This is a good point and might help readers get a sense of how expensive the method is - we will add numbers to the next draft.
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# Summary
Your suggestions have led to **improved clarity** (via the many points - thank you for them!), as well as **strength of evaluations** of this work. Given these additions and above clarifications, we would gently like to ask whether you would consider increasing your score.
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Rebuttal Comment 1.1:
Comment: Thanks for the detailed rebuttal! I appreciate that the authors ran additional experiments. That said, I'll keep my "weak accept" assessment.
I still find the paper interesting and the technique promising, but the lack of quantitative results still affects clarity. The rebuttal mentions further experiments in line with my suggestions but only provides rough summaries, not concrete setups or results -- just a promise to include numbers in the next draft. Including tables or figures in the rebuttal would have made it easier to assess the changes.
Again, I thank the authors for the rebuttal. I still like the submission and will keep my (already positive) score.
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Reply to Comment 1.1.1:
Comment: Thank you! Unfortunately, as we were character-limited in our response above, we had to keep the description of the additional comparisons we have performed brief. Here's a more-detailed description of the additional experiments and preliminary results:
1. **SGD vs. Cholesky** [complete]:
We took a scene consisting of the Scorpion mesh, then compute the posterior using both SGD and Cholesky factorization for the GP solve. We found that SGD typically converges to the solution found by Cholesky in about 1000 iterations. We also found, using a length scale that is too large (but not so large that factorization outright fails), that Cholesky factorization can produce poor-quality solutions which do not visually resemble the mesh. On the other hand, SGD is still able to find good solutions in this regime, and is less sensitive to the precise length scale value used for larger length scales.
2. **Amortization Grid Density** [complete]:
We evaluated reconstruction of the Armadillo mesh, using a titan of 5^3, 9^3, 17^3, and 33^3 points for the amortization grid density (following Sec. 3), and compute the posterior under each one. We find, visually, that using smaller grid densities leads to a loss of high-frequency details in both the reconstruction and in the variance used to represent uncertainty.
3. **Runtime Comparisons** [complete for input sensitivity]:
We measure how long both our algorithm and the SPSR baseline take, on a wall-clock basis, for performing reconstruction on the Stanford Dragon mesh as a function of the number of input points. For the former, we find that using 64 points takes 15 seconds (much of it we suspect due to Python overhead), 4096 points takes about 30 seconds, and using 65536 points takes about 5 minutes. We will add a plot showing these, and an additional comparison involving the number of output points.
4. **Next View Planning** [to be added]:
We will simulate progressive scans using both the camera score introduced by the SPSR paper, and the one we introduce in Sec. 3.4. At each time, we will take the mean reconstruction, display it, and additionally provide a quantitative comparison using the Chamfer distance to the ground truth mesh. | Summary: In the paper, the authors reformulated the stochastic Poisson surface reconstruction by introducing geometric Gaussian processes and periodic kernels. Their proposed method achieves similar results while addressing a number of limitations to increase computational efficiency.
Claims And Evidence: The claims made in the submission should have been supported by evidence.
Methods And Evaluation Criteria: Not sure. As a paper introducing a new Poisson surface reconstruction method, there are no quantitative evaluations and comparisons of reconstruction quality.
Theoretical Claims: The proof for theoretical claims should be correct.
Experimental Designs Or Analyses: Overall, the experimental designs and analyses are sound.
Supplementary Material: Yes, the supplementary material provides proposition verification, experimental details and additional results.
Relation To Broader Scientific Literature: The paper introduces an advanced surface reconstruction methodology.
Essential References Not Discussed: All essential references should have been discussed.
Other Strengths And Weaknesses: I find little weakness in the paper overall. It is appreciated that the authors also demonstrate various applications of their method. However, as a method focused on reconstructing surfaces from point clouds, the paper does not directly compare the reconstruction quality and runtime with other approaches. Additionally, the paper only compares its approach with a single baseline, which appears to be somewhat limited. It fails to provide a clearer understanding of the method's efficiency and accuracy relative to existing techniques.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review! We appreciate your recognition that our approach **“increase[s] computational efficiency”** and that our paper has **“little weakness”** and are **delighted by these comments**! We address your key comments below:
> “no quantitative evaluations and comparisons of reconstruction quality”
> “However, as a method focused on reconstructing surfaces from point clouds, the paper does not directly compare the reconstruction quality and runtime with other approaches”
> “Additionally, the paper only compares its approach with a single baseline, which appears to be somewhat limited”
These comments, while brief, are also quite important: let us address them in some detail. First, let us **draw attention to the following subtle distinction between tasks**:
1. **“Surface reconstruction”**: given a point cloud, produce a reconstructed surface
2. **“Uncertainty quantification for surface reconstruction”**: given an underlying surface reconstruction algorithm, and noisy or otherwise imperfect inputs, produce an estimate of uncertainty for the reconstructed surface
From this viewpoint, **our proposed algorithm’s purpose is 2 - that is, uncertainty quantification for surface reconstruction**, where the “underlying surface reconstruction algorithm” is classical PSR (or more precisely, a minor variant thereof, given our slightly-different boundary conditions).
As such - and given that algorithms of this kind are rather new - **SPSR is the only appropriate baseline we are aware of**. Mirroring the standard used in that work - and more broadly in graphics - our results focus on qualitative behavior, though we agree more quantitative comparisons would make the paper stronger.
To achieve this, in addition to the quantitative results that we currently have - such as runtime performance benchmarks - we have **performed additional evaluations such as hyperparameter comparisons** (as requested by other reviewers and described in our responses there). In addition, inspired by the need to quantitatively evaluate uncertainty in a manner fitting the above framing, we will also **add a quantitative benchmark of our next-view planning heuristic** (compared to SPSR baseline), following the setup in Figure 15 of "Neural Stochastic Screened Poisson Reconstruction", Sellán and Jacobson, SIGGRAPH Asia 2023 (which studies the more-general screened Poisson surface reconstruction setting). We anticipate to complete this by the next manuscript draft.
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# Summary
Overall, your suggestions have led us to **significant improvements, especially in clarifying appropriate positioning** for this paper, but also in the right way to handle quantitative comparisons. On behalf of these additions - including extra experimental results described in our responses to other referees, which were inspired in part by points that became apparent to us through your review - we would gently like to ask whether you would consider increasing your score. | null | null | null | null | null | null |
Rectifying Conformity Scores for Better Conditional Coverage | Accept (poster) | Summary: The paper presents a novel method to achieve better conditional coverage in conformal prediction for single-output and multi-output regression. The central idea is to start from a classical nonconformity score, and adjust it to improve for conditional coverage. The adjustment is a factor that is obtained by estimating conditional quantiles using classical or local quantile regression.
The authors present theoretical results, claiming that their proposed method achieves the desired marginal and conditional coverage, provided that conditional quantiles are known.
The experiments on synthetic and real-world data intend to show that the proposed method works well in practice. On real-world datasets improvements in conditional coverage are observed compared to four baseline methods.
Claims And Evidence: The main goal of the paper is to present a new method that improves on conditional coverage.
I believe that the presented method is novel, but it is a pity that the authors don't discuss the limitations of their approach.
I enjoyed reading the theoretical discussion in Section 3, but I am somewhat less convinced of the practical implementation in Section 4. Conformalized quantile regression has been proposed in the literature as a tool to improve the quantiles obtained by quantile regression, so that better conditional coverage is obtained. Here the authors are reasoning the other way around: they are using quantile regression to improve what conformal prediction is doing wrong... So, others have claimed that quantile regression is not good in obtaining quantiles for regression problems that are strongly heteroskedastic, while here is claimed that quantile regression is the solution. I believe that this deserves more discussion...
In light of this, the experiments with synthetic data are also not convincing. It is obvious that conditional coverage will be obtained if access to the ground-truth conditional distribution is assumed. I would have liked to see on synthetic data how the method performs when the quantiles need to be estimated using quantile regression. The considered toy problem is strongly heteroskedastic, so I assume that estimating the quantiles is far from trivial, despite the one-dimensionality of the problem in feature space.
Apart from the connection with conformalized quantile regression, I believe that the proposed method is also closely related to the "normalized" conformal prediction literature. This literature is not discussed in the related work section, but normalized nonconformity scores have a very similar idea in mind. For regression, the standard nonconformity score based on absolute residuals is divided by (an estimate) of the variance, see e.g.:
H. Papadopoulos, A. Gammerman, and V. Vovk. Normalized nonconformity measures for regression conformal
prediction. In Proceedings of the IASTED International Conference on Artificial Intelligence and Applications
(AIA 2008), pages 64–69, 2008.
U. Johansson, H. Boström, and T. Löfström. Investigating normalized conformal regressors. In 2021 IEEE
Symposium Series on Computational Intelligence (SSCI), pages 1–8. IEEE, 2021.
N. Dewolf, B. De Baets ,and W. Waegeman, Conditional validity of heteroskedastic conformal regression. Arxiv 2023.
Under certain assumptions, exact conditional coverage is obtained, similar to the reasoning of the authors. So, I think that this literature should be discussed. Moreover, normalized conformal prediction would also be the most obvious baseline in the experiments. Conformalized quantile regression would also be an obvious baseline. I did not understand the reasoning of the authors for the baselines they chose.
Methods And Evaluation Criteria: See previous section.
Theoretical Claims: The theoretical claims make sense to me. I did not check the proofs in detail, but the claims are pretty straight-forward, so I don't see issues.
I don't understand why assumption H2 is needed. This is a very general assumption that is always fulfilled in practice, isn't it? Perhaps this assumption can be simply omitted.
Experimental Designs Or Analyses: See above.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: See above.
Essential References Not Discussed: See above.
Other Strengths And Weaknesses: Strengths:
- The paper is very well written (the authors give evidence of a solid math background, which is appreciated)
- The proposed method is novel
- The authors present non-trivial theoretical results
Weaknesses:
- The limitations are not discussed
- Related work is missing
- The experiments are a bit underwhelming.
Other Comments Or Suggestions: None.
Questions For Authors: I invite the authors to give feedback on my comments.
Ethical Review Concerns: No
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thorough and constructive feedback, which helps improve our manuscript. Below, we address your valuable points:
The **main limitations** of RCP can be summarized as follows:
- The quality of the prediction regions heavily depends on the basic conformity score $V$. For example, if the underlying multi-output conformal method predicts hyperrectangular sets, RCP will also predict hyperrectangular sets.
- The quality of the conditional coverage of the intervals crucially depends on the quality of the conditional quantile estimator $\hat{\tau}(x)$ of the conformity score. The marginal coverage guarantee is **always ensured**; however, the guarantee of conditional coverage clearly depends on how $\hat{\tau}(x)$ approaches $\tau_*(x)$, the "exact" quantile. A key contribution of our work is the explicit tracking of how errors in quantile estimation influence conditional coverage error.
**Additional experiment on synthetic data.** Following your advice, we conducted an additional experiment on synthetic data to investigate the case of learned quantile estimate. We used a simple MLP trained on a dataset of varying sizes ranging from 100 to 500 points (note that the calibration dataset size in this experiment is equal to 500). The resulting plot can be found via https://pdfhost.io/v/ND3Dt3PahY_Additional_synthetic_data_experiment
We see that the conditional coverage is not perfect, but RCP outperforms the standard CP already for a relatively small data size of 100 points.
**Why assumption H2 is needed?** This assumption ensures that the score function is compatible with the adjustment function. Only valid $t$ values will be supplied to $f\_t(v)$ to ensure that H1 is satisfied. For example, if $f_t(v)=tv$ then $\hat{\tau}(x)$ has to be positive.
**Connection with normalized conformity scores.**
There is indeed a connection to prior works on normalized conformity scores. We will incorporate these references into the literature review of the camera-ready version (if accepted). Normalized Conformity Scores (NCS) all share the core idea of normalizing nonconformity scores by the predictive accuracy of the underlying model at new data points. This normalization aims to enhance the efficiency of conformal predictions by assigning wider prediction intervals to challenging instances and narrower intervals to easier ones, with the difficulty determined by the accuracy of the predictive model itself. However, these studies generally lack a detailed analysis of approximate conditional coverage, which distinguishes our work. Furthermore, we can recover the specific formulation of normalized nonconformity scores through an appropriate choice of the function $f_{\tau}(v)$. However, the criterion employed in our method to estimate $\hat{\tau}(x)$ fundamentally differs.
We provide further details below.
- U. Johansson et al. [1] and Papadopoulos et al. [2] investigate NCS methods, which enhance standard conformal prediction by dynamically adjusting prediction interval sizes according to instance difficulty. Normalization in their methods involves a parameter $\beta$, which balances the model's prediction error and the estimation of difficulty. However, these methods lack explicit theoretical guarantees. Their NCS can be represented within our framework through a specific choice of the function $f_{\tau}(v) = v/(\tau + \beta)$. Notably, the estimation approach employed in these papers uses least-squares regression on residuals, in contrast to the quantile regression approach adopted in RCP. The central goal in RCP is to construct a "rectified" conformity score that aligns conditional and unconditional quantiles at a target level--an objective distinct from NCS.
- The paper by Dewolf et al. [3] provides an insightful summary of normalized conformal predictors, introducing the concept of a taxonomy function, which they assume to be discrete. In their own terms, the taxonomy function "divides the instance space based on an estimate of the uncertainty," for example, by partitioning the feature space through binning the (conditional) standard deviation. However, their analysis is restricted to an oracle setting, meaning that the theoretical developments rely on an exact, known normalizing function. Consequently, their work does not address the practical scenario in which this normalizing function must be estimated from data.
[1] H. Papadopoulos, A. Gammerman, and V. Vovk. Normalized nonconformity measures for regression conformal prediction. In Proceedings of the IASTED International Conference on Artificial Intelligence and Applications (AIA 2008), pages 64–69, 2008.
[2] U. Johansson, H. Boström, and T. Löfström. Investigating normalized conformal regressors. In 2021 IEEE Symposium Series on Computational Intelligence (SSCI), pages 1–8. IEEE, 2021.
[3] N. Dewolf, B. De Baets ,and W. Waegeman, Conditional validity of heteroskedastic conformal regression. Arxiv 2023. | Summary: The paper considers the problem of producing conformal prediction sets with conditional guarantees. The idea is to rectify non-conformity scored by to use additional hold out data to fit a quantile regressor that is then applied to the non-conformity score. Marginal coverage guarantees are obtained using the remaining part of the data to run split cp on the rectified nc scores.
Claims And Evidence: The paper claims to improve conditional coverage compared to existing schemes; however, as shown in the Appendix the proposed method has very similar performance to well established methods as CQR and it is not compared to methods such as those presented in Conformal prediction with conditional guarantees by Gibbs, I., Cherian, J. J., and Candes, E. J., and Boosted Conformal Prediction Intervals by R Xie, R Barber, E Candes.
Methods And Evaluation Criteria: Yes, benchmarks make sense.
Theoretical Claims: The theoretical claims appear to correct as they follow from the properties of split cp which is applied to the rectified scores. What are the technical challenges and novelty that the current analysis brings?
Experimental Designs Or Analyses: Yes, experiments are correct. However I believe that other baselines (CQR) should be either moved to the main text and additional ones considered (such as those mentioned above based on boosting, conditional coverage and conformal training should be included.
Supplementary Material: Yes, I have read the additional simulations and proofs.
Relation To Broader Scientific Literature: I think the paper does a good job at highlighting similarities with existing literature; however I believe it misses on discussing conformal training methods.
Essential References Not Discussed: The idea of optimizing the non-conformity score for improved efficiency and conditional coverage is common in conformal training and CP length optimization. See:
Large language model validity via enhanced conformal prediction methods by John J. Cherian, Isaac Gibbs, Emmanuel J. Candès
Kiyani S, Pappas GJ, Hassani H. Length optimization in conformal prediction. Advances in Neural Information Processing Systems.
R Xie, R Barber, E Candes, Boosted Conformal Prediction Intervals
Other Strengths And Weaknesses: I think the idea is simple, but that is not necessarily a weakness of the paper. However, I had trouble understanding the benefits and novelty of the proposed scheme compared to existing methods such as CQR, conformal training, and conditional coverage methods. This concern arises from the fact that these methods are either not benchmarked or, in the case of CQR, have similar or superior performance to the proposed one (e.g., in Figure 9, CQR has the same conditional coverage but a smaller volume?)
Other Comments Or Suggestions: I have found problems following the methodology section given that at some point is set f_t(v)=\tilde f_v(t). Is this really necessary?
Questions For Authors: What is exactly the technical novelty and benefits of the proposed method as compared to the above mentioned schemes? How do they empirically compare?
Update after rebuttal: I have decided to update my score from reject to weak reject. There exists a fairly large number of relevant papers that are not discussed or benchmarked. This is a common concern among other reviewers; however, they did not consider it as serious as I did—hence my score upgrade.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We acknowledge the critical feedback and aim to address the raised points. Below we clarify why **the undiscussed references, while indeed valuable, mostly address aspects different from the specific problem we focus on**. The following discussion highlights the distinctive advantages of our RCP method for constructing confidence sets in multivariate prediction, offering exact marginal coverage and strong theoretical guarantees for conditional coverage.
**Discussion of the references provided in the review.**
- Among the papers cited, Gibbs et al. (2023) is the one most directly related to our work, as it acts as a wrapper on given conformity scores. It has already been discussed, but additional comments and experiments are worthwhile. From a computational point of view, their method (called CPCG below) is very intensive, mainly because the wrapper uses a form of the "full conformal" idea, which requires solving an optimization problem at test time. Its strength lies mainly in finite-sample guarantees tailored explicitly to specific feature subsets and covariate shifts (see Theorem 2 for finite-dimensional class). This targeted approach suits group conditional coverage (Corollary 1) well. In contrast, RCP uses a split-conformal idea that estimates a quantile function on a special subset of the data, which greatly improves computational complexity. Also, for RCP, we provide a more generic theoretical result that is agnostic to a particular estimation method used (Theorem 4), and also specify it for the case of local quantile regression (Proposition 5). The proof of the results is not straightforward and requires the usage of non-trivial technical tools such as very recent extensions of DKW inequality (see Lemma 16).
- Cherian et al. (2024) is a CP framework tailored for LLMs. The method is not easily applicable to conventional regression or standard multivariate classification scenarios, where more broadly effective methods like RCP are more natural.
- Xie et al. (2024) refine conformity scores via gradient boosting to enhance conditional coverage while achieving exact marginal coverage in univariate prediction models. This method is constrained to scalar outcomes and lacks a natural extension to multidimensional settings. Further, the lack of analytically interpretable theoretical guarantees on conditional coverage and reliance on numerous hyperparameters and differentiable approximations complicates both theoretical understanding and practical implementation.
- Kiyani’s (2024) CPL method combines conditional validity and optimized efficiency through constrained optimization, designed exclusively for univariate prediction intervals. While CPL provides exact coverage tailored for a specific class $\mathcal{F}$, it is fundamentally limited by its complexity. Specifically, the reliance on intricate optimization procedures limits broader practical application, especially for multivariate outputs. In contrast, RCP’s computational simplicity and broader versatility in handling multivariate scenarios position it distinctly ahead.
Thus, among these methods, RCP clearly emerges as superior, particularly in multivariate predictive contexts. It balances precision in conditional coverage with practical simplicity, computational efficiency, and broader applicability.
**Empirical comparison with CQR and CPCG.** We conducted an additional experiment to directly compare RCP and CPCG (see https://pdfhost.io/v/26gN4fUeS2_rebuttal-R3jf).
We observe that CPCG and RCP give similar conditional coverage, while RCP is at least two orders of magnitude faster. Compared to CQR, it trains a quantile regression model directly on the whole training set, while RCP can be applied to any black-box model and does not require access to the training data or internal model structure. Figure 10 shows that RCP can match or outperform CQR in a multidimensional setting.
**Technical novelty.**
The **technical novelty** of RCP lies in its approach to enhancing conditional coverage through the concept of "rectifying" conformity scores. Unlike conventional methods requiring estimating the entire conditional distribution for multivariate predictions, RCP simplifies the problem by calculating only the conditional quantile of a univariate conformity score. This quantile estimation is a wrapper around classical methods explicitly tailored for multivariate prediction sets. Furthermore, RCP provides explicit theoretical lower bounds on conditional coverage, directly linking prediction accuracy to the quantile estimation approximation error. These results are based on careful and non-trivial analysis as discussed above. **While competitive methods exist for univariate predictions, such comparisons are irrelevant, as univariate scenarios are explicitly not our targeted application**. Thus, our proposed RCP method represents a **meaningful advancement**, combining clear theoretical foundations with practical efficiency for multivariate prediction tasks.
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Rebuttal Comment 1.1:
Comment: Thank you for having taken the time to address my comments!
Regarding the relevance of Kiyani’s and Cherian’s work, it lies in the fact that their approaches optimize a parameterized non-conformity scoring function to improve efficiency and conditional coverage. In that sense, the idea of “rectifying” non-conformity scores by choosing within a family of parametric transformations, as RCP does, is related.
However, I don’t understand why previous literature is completely disregarded, given that it is claimed to be limited to uni-dimensional target variables. Many of the mentioned alternatives operate directly on the non-conformity scoring function, making them independent of the target’s dimensionality. Once a non-conformity scoring function is established—even for multidimensional targets—the methods proposed by Kiyani and Cherian still apply. The same principle holds for simpler methods, such as variance-reduced (or normalized) non-conformity scores, where errors are simply divided by the average. The gap between unimodal and multimodal approaches isn’t just about replacing absolute values with norms, is it? Consider the work of Colombo "On training locally adaptive CP". Aren't all the proposed transformation applicable to this setting by simply the norm error $\lVert f(X)-Y\rVert$, instead of the absolute error?
In my original reply, I mistakenly referred to Figure 10 as Figure 9. However, the concern remains. How do you conclude that RCP outperforms CQR based on this figure? RCP outperforms CQR in only four datasets and is outperformed by CQR in two. I would not conclude that one method consistently outperforms the other. The same applies to conditional coverage—there is no clear winner in that metric either.
Thanks again for taking the time to write the rebuttal and provide the additional experiments.
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Reply to Comment 1.1.1:
Comment: Dear reviewer R3jf,
we thank you for your comments and address your remaining questions and concerns below.
1. We strongly disagree with the assertion that previous literature has been completely disregarded; on the contrary, our work makes extensive reference to relevant previous studies (among the 60+ references, more than 40 are recent - less than 10 years). The literature on conformal methods is extraordinarily vast, and conducting a concise state-of-the-art review inherently requires deliberate selection and prioritization. In this paper, we have intentionally focused on the most prevalent and widely adopted approaches, particularly those we evaluate directly through our benchmarks. We maintain that our selection contains no significant omissions. Nevertheless, we acknowledge the potential relevance of additional contributions and elaborate further on this point below. We will also do it in a final version of the paper.
- The works by **Cherian and Kiyani** are indeed valuable contributions; however, their conditional coverage guarantees are restricted to specific classes of functions. Consequently, these methods do not achieve the same form of pointwise approximate conditional coverage that we establish in our approach. While it is appropriate to acknowledge these references within our literature review, a direct empirical comparison is not feasible due to fundamental differences in methodological setups and underlying assumptions.
- The paper by **Colombo** is indeed highly relevant, and we agree that it is appropriate to explicitly include it in our discussion. We thank the reviewer for drawing our attention to this reference. However, we emphasize that the method proposed by Colombo differs substantially from RCP, as discussed in detail below. RCP proposes utilizing a modified score defined as $\tilde{V}(x,y)=f_{\hat{\tau}(x)}^{-1}(V(x,y))$, where $\hat{\tau} (x)$ is estimated using a separately held-out dataset. Colombo et al. instead use $\tilde{V}(x,y)=\phi_{x}(V(x,y))$ and a specific conformity score $V(x,y)=a(f(x),y)$, where $f$ is a pre-trained point prediction model.
While it may appear appealing to interpret our approach simply as a particular case of the general formulation $\phi_x=f_{\hat{\tau}(x)}^{-1}$, this characterization is is not correct. First, the score transformation we propose is fundamentally different: it is also adaptive, but the objective is different. The method by Colombo directly optimizes the size of the prediction set. The key idea behind our method is to ensure that, at a given user-defined confidence level $(1-\alpha)$ the conditional and the unconditional quantile of the rectified conformity score matches (as discussed in Section 3 of our paper). Thus, standard estimation methods for conditional quantiles regression can be directly employed - as well as the most of the classical theory of conditional quantile regression. Second, Colombo's approach does not establish conditional coverage guarantees, and obtaining such guarantees within their methodological framework appears to pose significant technical challenges.
2. We regret that our original formulation of the motivation was insufficiently clear, as it has evidently given rise to some misunderstanding. To clarify, **we do not view multivariate prediction problems simply as straightforward extensions of the univariate setting**, achievable by merely substituting a norm for an absolute value. Our method is applicable to any score function and we aimed to contrast it with the methods that are inherently specialized to the one-dimensional case, such as CQR, which explicitly constructs prediction intervals and necessitates full access to training data for retraining the predictive model (like in [1,2] among many others). In contrast, the practical scenarios we consider involve multi-dimensional data and rely on a pre-existing "black-box" predictor, with no access to the original training data, thus precluding any fine-tuning or retraining of the underlying predictive model.
3. Regarding **experimental concerns**, we appreciate the reviewer's viewpoint regarding Figure 10; however, we should note that it shows the results for the weaker RCP methods than we have in the main part of the paper. To better demonstrate the benefits of RCP over CQR, we compare it with stronger methods , namely RCP-DCP and RCP-PCP. https://pdfhost.io/v/J9vFWdNcWC_R3jf shows that RCP-DCP and RCP-PCP obtain smaller region sizes while achieving competitive conditional coverage.
Therefore, considering both the theoretical foundations and the practical performance demonstrated by RCP, we believe our experimental results substantiate the clear benefits of our approach.
[1] Boström, H. et al. Accelerating difficulty estimation for conformal regression forests. Annals of Mathematics and Artificial Intelligence, 2017.
[2] Cabezas, L. M. et al. Regression trees for fast and adaptive prediction intervals. Information Sciences, 2025. | Summary: This paper introduces Rectified Conformal Prediction (RCP), a novel method for improving conditional coverage in conformal prediction while maintaining exact marginal coverage. The core idea is to transform conformity scores in a way that aligns their conditional quantiles across different covariates. This transformation is achieved by estimating the conditional quantile of conformity scores and using it to rectify the scores before applying the standard conformal prediction procedure. The authors establish theoretical guarantees for the proposed method, including a lower bound on conditional coverage that depends on the accuracy of the quantile estimate. The paper also presents experimental results demonstrating that RCP outperforms existing methods in achieving improved conditional coverage while retaining valid marginal guarantees.
Claims And Evidence: The paper provides a well-structured theoretical justification for its claims. The derivation of the conditional coverage bound appears mathematically sound, and the authors clearly articulate how their method improves over traditional approaches. The empirical validation is extensive, comparing RCP against multiple existing conformal prediction techniques across synthetic and real-world datasets. However, while the paper provides strong empirical evidence, the effectiveness of the quantile estimation technique is not thoroughly explored in more complex, high-dimensional settings. Additionally, the impact of the choice of transformation function ft on different types of datasets could have been analyzed in more depth.
Methods And Evaluation Criteria: Yes, the benchmark datasets used in the experiments are well-chosen. The paper includes synthetic datasets to illustrate theoretical properties and real-world regression datasets to validate practical performance. The use of worst-slab coverage and conditional coverage error as evaluation metrics is appropriate for measuring improvements in conditional validity. However, additional experiments with more challenging multivariate distributions could have further strengthened the empirical evaluation.
Theoretical Claims: The theoretical results presented in Section 6 appear to be correctly derived. The proof of Theorem 3 for marginal coverage follows standard conformal arguments. The bound on conditional coverage (Theorem 4) correctly incorporates the accuracy of the conditional quantile estimate, and the derivations align with known results from quantile regression literature. However, I did not rigorously verify all steps in the Appendix proofs.
Experimental Designs Or Analyses: The experimental setup is methodologically sound:
The authors compare RCP against multiple state-of-the-art conformal methods (e.g., ResCP, PCP, SLCP, DCP).
They use a standard train-validation-test split and ensure calibration data is separated from test data.
The quantile estimation methods (neural networks and local quantile regression) are well-justified.
The choice of transformation functions for conformity scores is systematically varied.
One concern is that the effect of incorrect quantile estimation on performance is not fully explored beyond the toy example. Understanding how estimation errors affect real-world datasets would be crucial for deployment in practical applications.
Supplementary Material: Yes, I reviewed the Appendices, which contain:
Additional theoretical proofs for the rectified transformation framework.
Extended experimental results, including different quantile estimation techniques.
Alternative transformation functions and their effect on coverage.
Relation To Broader Scientific Literature: The paper builds upon the conformal prediction framework, particularly methods that aim to approximate conditional validity. Prior work has either:
Partitioned the covariate space (leading to inefficient large prediction sets) or
Reweighted empirical distributions (which struggles in high dimensions).
The paper’s key novelty is the idea of rectifying conformity scores through a learned transformation, making conditional quantile estimation more tractable. This idea is conceptually related to:
Conformalized Quantile Regression (CQR) (Romano et al., 2019).
Localized Conformal Prediction (Guan, 2023).
Compared to these works, RCP introduces a more flexible and computationally efficient alternative that does not require explicit conditional density estimation.
Essential References Not Discussed: The paper does a good job of referencing key works in conformal prediction, including classical results (Vovk, 2005) and recent advances (Angelopoulos et al., 2023). However, some more recent studies on uncertainty quantification could provide additional context:
Training-Conditional Coverage Methods (Bian & Barber, 2023) discuss techniques that could potentially be adapted into RCP.
Other Strengths And Weaknesses: Strengths:
The conceptual novelty of rectifying conformity scores is a valuable contribution to conformal inference.
The theoretical guarantees are rigorously derived and provide a meaningful lower bound on conditional validity.
The experiments are thorough, with comparisons across multiple datasets and methods.
The approach is computationally efficient and avoids the pitfalls of full conditional density estimation.
Weaknesses:
The quantile estimation step is critical to the method, but the authors do not explore the trade-offs between different estimation strategies in high-dimensional settings.
The impact of outliers in score rectification is not well analyzed.
The choice of transformation function ft is somewhat arbitrary, and more discussion is needed on selecting appropriate transformations for different problem domains.
Other Comments Or Suggestions: Section 4: "tau(x)" is sometimes written inconsistently.
Section 6, Theorem 4: The notation "L" for Lipschitz continuity should be explicitly defined earlier.
Figures 3 & 4: Labels should include dataset sizes for better context.
Questions For Authors: How does RCP perform when the conditional quantile estimator is misspecified? The toy example considers synthetic noise, but what about real-world miscalibration?
What is the computational cost of different transformations? Are some ft transformations significantly more expensive than others?
Could the framework be extended to sequential settings? For example, how would RCP adapt in online learning scenarios?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thorough and constructive feedback, which helps improve our manuscript. Below, we address your valuable points:
**Effectiveness of quantile estimation in high-dimensional settings:**
Indeed, quantile estimation accuracy critically affects RCP performance. In our experiments, we selected neural networks and local quantile regression specifically due to their scalability to higher dimensions. However, we acknowledge that our explicit evaluation in very high-dimensional regimes remains limited. Following your suggestion, we will include additional discussions and empirical results to better highlight performance and trade-offs in higher-dimensional settings.
**Choice of the transformation $f_t$** There are numerous possible choices for the function \\( f_t \\). Thus far, we have always restricted ourselves to relatively simple transformations, often inherited from the literature on "normalized conformity scores," which we recognize should have been more thoroughly credited. We believe it is important that the proposed method remains simple and does not rely on hyperparameters, ensuring that the computational cost of this wrapper stays reasonable.
**Additional experiments with challenging multivariate distributions:**
We appreciate your suggestion for extending experiments to more complex multivariate distributions, as this would further reinforce our empirical validation. However, our current synthetic and real-world examples demonstrate clear advantages, while the datasets have dimensions up to 16. In our revised submission, we will incorporate an experiment that highlights RCP’s behavior on more challenging multivariate datasets.
**Impact of incorrect quantile estimation:**
We agree that understanding the impact of incorrect quantile estimation beyond synthetic noise is crucial. To address your comment, we plan to include a detailed analysis showing how estimation errors affect coverage in more realistic settings, thereby providing deeper insights into RCP’s robustness and practical utility.
**Extension to sequential settings:**
Your question regarding sequential adaptation is insightful. While we had not previously explored this application, we find it highly promising. There are no conceptual or methodological difficulties; however, from a theoretical standpoint, everything remains to be developed. RCP’s framework naturally extends to online learning by sequentially updating the quantile estimator based on newly observed data. We envision future work that formally explores sequential conformal adaptations and briefly outline such potential directions in our revision.
**Clarification of minor points:**
- We will correct inconsistent notation for \\(\\hat{\\tau}(x)\\) throughout Section 4.
- The Lipschitz constant "L" in Theorem 4 will be explicitly defined earlier to improve readability.
- Figures 3 & 4 will indicate dataset sizes in the revised manuscript for enhanced clarity.
We appreciate your recognition of RCP’s conceptual novelty and theoretical rigor and your acknowledgment of our thorough experimental evaluation. Your suggestions significantly strengthen the manuscript, and we will diligently incorporate these improvements.
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Rebuttal Comment 1.1:
Comment: i thank the authors for the response and I will maintain my positive score. | Summary: This paper introduces Rectified Conformal Prediction (RCP), a novel framework for improving conditional coverage in conformal prediction while preserving exact marginal validity. The key idea is to learn a transformation of the conformity score such that the ($1-\alpha$)-quantile of the transformed score becomes covariate-independent. This is done by estimating the conditional quantile of a transformed conformity score and applying a local re-scaling (or shifting) to normalize variability across the feature space. The authors provide theoretical guarantees on marginal and approximate conditional validity, demonstrate the flexibility of the framework across multiple conformity scores and predictors, and show empirical improvements over state-of-the-art methods across synthetic and real-world regression datasets.
Claims And Evidence: Most of the claims in the submission are supported by clear and convincing evidence, particularly the theoretical guarantees for marginal validity and approximate conditional coverage. The empirical results convincingly demonstrate improved conditional coverage across a range of regression tasks, validating the main claim that the proposed rectification improves local adaptivity. However, the paper lacks evaluation on coverage–efficiency tradeoffs.
Methods And Evaluation Criteria: 1. RCP's conditional coverage guarantee hinges on accurate estimation of $\tau^*(x)$. How sensitive is RCP to misspecification of the quantile regressor? Could you show examples where quantile regression underperforms and discuss failure modes?
2. RCP estimates a single quantile per point. How would RCP handle two-sided intervals (e.g., $[Q_{\alpha/2}(x), Q_{1 - \alpha/2}(x)]$)?
Theoretical Claims: 1. How restrictive are the assumptions about monotonicity and invertibility of the transformation functions? Can your method handle scores with negative values (e.g., log-likelihoods) without heuristic adjustments?
2. The bound in Theorem 4 depends on Lipschitz continuity of the quantile mapping. Can you elaborate on how often this assumption holds in practice? Can you provide empirical values of the bound components?
Experimental Designs Or Analyses: 1. The paper lacks evaluation on coverage–efficiency tradeoffs. Do RCP sets tend to be wider due to more cautious calibration?
2. The framework requires choosing a transformation $f_t$ and tuning quantile regression models. How sensitive is performance to these choices? Could you provide ablations?
Supplementary Material: I did not review the supplementary code as part of my evaluation. My review is based on the theoretical justifications, experimental results, and clarity of the main paper.
Relation To Broader Scientific Literature: The paper builds on and extends works in conformal prediction, particularly methods aimed at improving conditional coverage. This paper proposes a transformation-based approach inspired by recent work on score adjustment and local calibration. It is closely related to conformalized quantile regression in that both seek to adapt prediction sets to local data properties, but RCP generalizes this idea by applying a trainable transformation to arbitrary conformity scores. While prior methods address heterogeneity via weighting or region-specific coverage, RCP’s novelty lies in aligning the conditional and marginal quantiles of transformed scores, thereby offering a new perspective on achieving conditional validity without relying on density estimation or rigid group partitions.
Essential References Not Discussed: The paper cites and discusses a wide range of essential related works, including classical methods for marginal coverage, approaches for approximate conditional coverage via stratification or grouping, and more recent developments.
Other Strengths And Weaknesses: Strengths:
1. The rectification strategy is modular and applicable to a variety of conformity scores and models.
2. The authors derive meaningful guarantees on conditional coverage as a function of quantile estimation error.
3. The paper evaluates on diverse multi-output regression datasets, including synthetic setups and real-world benchmarks.
4. The paper is mostly well-written and easy to follow.
Other Comments Or Suggestions: This paper uses lots of math notations. I suggest the authors summarize the math notations in a table.
Questions For Authors: 1. RCP's conditional coverage guarantee hinges on accurate estimation of $\tau^*(x)$. How sensitive is RCP to misspecification of the quantile regressor? Could you show examples where quantile regression underperforms and discuss failure modes?
2. RCP estimates a single quantile per point. How would RCP handle two-sided intervals (e.g., $[Q_{\alpha/2}(x), Q_{1 - \alpha/2}(x)]$)?
3. How restrictive are the assumptions about monotonicity and invertibility of the transformation functions? Can your method handle scores with negative values (e.g., log-likelihoods) without heuristic adjustments?
4. The bound in Theorem 4 depends on Lipschitz continuity of the quantile mapping. Can you elaborate on how often this assumption holds in practice? Can you provide empirical values of the bound components?
5. Have you evaluated the size of the prediction sets produced by RCP compared to standard CP or CQR? Do RCP sets tend to be wider due to more cautious calibration?
6. The framework requires choosing a transformation $f_t$ and tuning quantile regression models. How sensitive is performance to these choices? Could you provide ablations?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thorough and constructive feedback. Below, we address your questions:
Q1: **RCP's conditional coverage guarantee hinges on accurate estimation ...** Even if the quantile regressor is misspecified, RCP’s conformal calibration guarantees valid marginal coverage by construction. Nevertheless, poor quantile estimates affect conditional coverage: underestimations yield local under-coverage, whereas overestimations produce overly conservative intervals. Such failure modes highlight that RCP inherits biases from quantile regression, reducing conditional efficiency despite correct marginal coverage. This sensitivity was illustrated in our synthetic experiments; additional examples and analysis will be provided.
Q2: **RCP estimates a single...** RCP computes quantiles of a nonconformity score and thus only concerns with the right tail of the distribution (when the nonconformity score gets large). Therefore, obtaining intervals with lower and upper quantile estimates is not typically needed. Note that for a one-dimensional prediction target, we can, of course, work with CQR-type interquantile intervals as a specific nonconformity score.
Q3: **How restrictive are the assumptions about monotonicity and invertibility of the transformation functions?** The monotonicity is essential for our approach as we insist on preserving the ordering of the conformity scores. After adjustment by a function with a fixed argument $\varphi$, a "large" nonconformity score must remain larger than a smaller one. Invertibility is a technical requirement that underlines our construction, but it is not as restrictive as the monotonicity assumption.
Q3: **Can your method...** the answer is yes. As an example, the adjustment function $f_t(v) = t + v$ does not restrict the range of scores. Specifically, it does not impose positivity or negativity constraints, thus naturally accommodating scenarios where the score can assume both negative and positive values. This flexibility is crucial for handling general scoring functions, ensuring applicability across a broad range of prediction tasks without additional transformations or restrictions.
Q4: **The bound in Theorem 4 depends on...** The Lipschitz property of the quantile function is standard in the statistical literature on conditional quantile estimation — see, for instance, the works [1,2] on this topic. It is difficult to delve into such subtle technical conditions in a short discussion. We will include a more substantial discussion of these contributions in the revised version.
[1] Y.K. Lee, E. Mammen, B. U. Park. "Backfitting and smooth backfitting for additive quantile models." 2010.
[2] M. Reiß, Y. Rozenholc, C. Cuenod. "Pointwise adaptive estimation for robust and quantile regression." arXiv:0904.0543. 2009.
Q5: **Have you evaluated the size...** Thank you for your suggestion. You're absolutely right — because RCP can generate larger sets for test instances with higher uncertainty, the resulting sets tend to have wider volume on average.
|dataset|PCP|RCP-PCP|DCP|RCP-DCP|ResCP|RCP-ResCP|
|--|--|--|--|--|--|--|
|scm20d|4.74e+07|1.01e+08|5.88e+06|1.16e+08|**2.50e+06**|6.20e+12|
|rf1|77.5|1.27e+03|**1.87**|6.87e+02|9.84|1.84e+08|
|scm1d|3.06e+06|2.17e+09|3.24e+06|1.00e+09|**1.47e+05**|7.17e+16|
|meps_21|2.31|4.41|**1.55**|2.40|5.73|6.82|
|meps_19|5.82|6.07e+03|**1.97**|6.71e+03|5.34|6.09e+06|
|meps_20|2.35|3.97|**1.48**|2.53|5.49|6.16|
|house|2.20|2.51|**1.89**|2.05|6.51|8.01|
|bio|0.823|1.05|**0.584**|0.630|1.14|1.38|
|blog_data|2.94|1.40e+05|**1.50**|1.80e+05|1.74|3.71|
|taxi|10.5|10.8|**6.94**|7.38|12.4|12.8|
However, when looking at the median volume, avoiding outliers, RCP outperforms baselines:
|dataset|PCP|RCP-PCP|DCP|RCP-DCP|ResCP|RCP-ResCP|
|--|--|--|--|--|--|--|
|scm20d|2.91e+06|**1.44e+06**|5.26e+06|3.26e+06|2.50e+06|1.37e+07|
|rf1|36.0|5.21|1.78|**1.09**|9.84|2.94|
|scm1d|2.72e+05|3.14e+06|2.57e+06|7.60e+05|1.47e+05|**3.36e+04**|
|meps_21|1.72|1.27|1.24|**1.03**|5.73|2.40|
|meps_19|2.60|1.22|1.32|**0.967**|5.34|2.43|
|meps_20|1.75|1.26|1.12|**0.968**|5.49|2.47|
|house|1.99|1.82|1.70|**1.60**|6.51|6.38|
|bio|0.717|0.689|0.530|**0.511**|1.14|0.927|
|blog_data|1.59|1.81|1.14|**1.08**|1.74|1.30|
|taxi|9.97|9.18|6.63|**6.24**|12.4|10.6|
We will report these metrics in Section 7.2.
Q6: **How sensitive is performance...** We discuss the sensitivity with respect to the choice of adjustment function in Appendices A.3-4. The choice has a significant influence on the results, as the ability of fixed single-parameter functions to rectify the results highly depends on the properties of the score distribution. An interesting future work is to design more flexible data-dependent adjustment functions. Sensitivity with respect to quantile regression is discussed in Appendix A.2, showing that a better fit of the quantile model improves the results. | null | null | null | null | null | null |
Robust Multimodal Large Language Models Against Modality Conflict | Accept (poster) | Summary: This paper investigates MLLM hallucination from a novel modality conflict perspective. Specifically, authors propose a setup where inputs from different modalities conflicts each other and put MLLMs in a dilemma. MLLMs are expected to address modality conflict first to answer correctly. A benchmark Multimodal Modality Conflict (MMMC) is proposed in this paper involving three visual aspects (i.e., object, attribute, relation). Authors evaluates three representative MLLMs and they find that these models cannot address modality conflicts well. They include three classical hallucination-mitigation approaches (i.e., prompt engineering, supervised fine-tuning and reinforcement learning), and carry out sufficient experiments to address modality conflict. They observe that reinforcement learning appears to be the most effective approach across various scenarios, which provides insights for future studies.
Claims And Evidence: The claims proposed in this paper are supported by clear and convincing evidence.
Methods And Evaluation Criteria: The proposed methods are sensical and sufficient enough and the evaluation criteria make sense.
Theoretical Claims: No theoretical claims are made in this paper.
Experimental Designs Or Analyses: The experimental designs in this paper are sufficient and technically sound. Especially, they do a wide range of explorations on addressing modality conflicts.
Supplementary Material: Yes. The supplementary material includes training details for Reinforcement Learning stage and model response examples.
Relation To Broader Scientific Literature: The paper relates to knowledge conflicts problem [1] from a broader scope, along with how it is addressed in some approach papers.
[1] Entity-Based Knowledge Conflicts in Question Answering. EMNLP 2021.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: The paper is pretty clear and technically sound in experiments.
Other Comments Or Suggestions: N/A.
Questions For Authors: N/A.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We truly appreciate your positive assessment of our paper. We are also grateful for the time and effort you invested in reviewing it. | Summary: This paper is well-written and presents a timely investigation into modality conflicts as an understudied source of hallucinations in multimodal large language models (MLLMs). The authors demonstrate commendable effort in constructing a comprehensive conflict dataset
spanning three critical dimensions (object, attribute, relationship) and empirically validating three baseline methods for hallucination mitigation.
Claims And Evidence: Yes, the claims in the submission are supported.
Methods And Evaluation Criteria: Yes, they make sense.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: The evaluation should include conflict-type-specific performance breakdowns, standard
benchmark comparisons pre/post training, or maybe chain-of-thought prompting baselines.
Supplementary Material: Yes, I reviewed all the supplementary materials.
Relation To Broader Scientific Literature: The paper's investigation of modality conflicts as a novel source of hallucinations in VLMs extends prior research on hallucination mitigation by addressing a critical gap in cross-modal interaction analysis.
Essential References Not Discussed: For the Knowledge Conflict, more essential references are required:
1. Knowledge Conflicts for LLMs: A Survey
2. ConflictBank: A Benchmark for Evaluating the Influence of Knowledge Conflicts in LLM
3. Adaptive chameleon or stubborn sloth: Unraveling the behavior of large language models in knowledge conflicts
Other Strengths And Weaknesses: strengths:
This paper is well-written and presents a timely investigation into modality conflicts as an
understudied source of hallucinations in multimodal large language models (MLLMs). The
authors demonstrate commendable effort in constructing a comprehensive conflict dataset
spanning three critical dimensions (object, attribute, relationship) and empirically validating
three baseline methods for hallucination mitigation.
weakness:
(1) The analysis lacks depth in disentangling the root causes. Fundamental questions remain
unanswered: Does hallucination primarily stem from the model's tendency to silently correct
user query errors? Or does it originate from vision encoders' failure to capture fine-grained
visual details?
(2)The proposed solutions (prompt engineering, SFT, RL) appear as direct adaptations of
existing techniques rather than modality-conflict-specific innovations, which need stronger
justification.
(3)The evaluation should include conflict-type-specific performance breakdowns, standard
benchmark comparisons pre/post training, or maybe chain-of-thought prompting baselines.
Other Comments Or Suggestions: This paper is well-written without any typos. I hope to see a deeper insight into the modal
conflicts.
Questions For Authors: See in part Weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We appreciate your insightful comments and suggestions. We give a point-by-point response to each of your concerns below. Following the ICML 2025 Peer Review FAQ, we post all additional results to the anonymous link: [https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305](https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305) for your reference.
**1. Other Strengths And Weaknesses**
Thanks for your valuable suggestions. We will add discussions about these papers your mentioned in the revised manuscript.
**2. The analysis lacks depth in disentangling the root causes. Fundamental questions remain unanswered: Does hallucination primarily stem from the model's tendency to silently correct user query errors? Or does it originate from vision encoders' failure to capture fine-grained visual details?**
Thank you for your insightful comments. Our work aims to uncover a fundamental source of hallucination, and while detailing every causal pathway is beyond our current scope, we conduct additional analysis based on our findings.
Firstly, we assert that the hallucination issue does not primarily arise from the model's inclination to silently correct user query errors. In our experiments utilizing a prompt engineering baseline, where the model is instructed to first ascertain the image content before addressing any queries based on that content, hallucinations still occur. In these scenarios, the model is expected not to correct any user errors, yet it frequently misrepresents image content.
Secondly, concerning the vision encoder's capability, MLLMs are generally pre-trained on extensive visual data [1,2], endowing their vision encoders with robust capabilities for recognizing fine-grained visual details. This is supported by their performance on standard benchmarks such as MMBench and MMMU, where the vision encoder has demonstrably captured intricate visual details successfully. Thus, it seems unlikely that hallucinations are due to a failure of the vision encoder in capturing these details.
Finally, we propose that the hallucination may stem from the model's inclination to prioritize certain data modalities when faced with conflicting information. Given the prevalent use of instruction-tuning in training MLLMs [1,2], models might develop a bias towards textual instructions over visual data. This predisposition can lead to hallucination, as the model may overly rely on textual information. We intend to incorporate this discussion in the revised manuscript and plan to conduct more rigorous analyses as part of future work.
[1] Liu, H., Li, C., Wu, Q., and Lee, Y. J. Visual instruction tuning. In *Proceedings of the Advances in Neural Information Processing Systems*, 2023.
[2] Wang, P., Bai, S., Tan, S., Wang, S., Fan, Z., Bai, J., Chen, K., Liu, X., Wang, J., Ge, W., Fan, Y., Dang, K., Du, M., Ren, X., Men, R., Liu, D., Zhou, C., Zhou, J., and Lin, J. Qwen2-VL: Enhancing vision-language model’s perception of the world at any resolution. *arXiv:2409.12191*, 2024.
**3. The proposed solutions (prompt engineering, SFT, RL) appear as direct adaptations of existing techniques rather than modality-conflict-specific innovations, which need stronger justification.**
The main focus of our work is to reveal the source of hallucination. Most potential modality-conflict-specific innovations would fall into the category of PE, SFT, RL, and the decoding-based method we just supplemented according to other reviewer's suggestion. Furthermore, the prompt template of PE and reward function of RL in this paper are specifically designed to tackle the modality conflict.
In spite of this, we are willing to provide some directions for improvement:
1. Incorporate external tools to detect the information in the image and text, and then use the detected information to guide the model to generate the answer.
2. Construct more fine-grained data, *e.g.*, annotating modality conflict by human, and then use the data to train the model.
We hope to attract more researchers to work on this challenging problem and provide deeper insights into the modality conflict.
**4. The evaluation should include conflict-type-specific performance breakdowns, standard benchmark comparisons pre/post training, or maybe chain-of-thought prompting baselines.**
We supplement the conflict-type-specific performance breakdowns in Table 2, 3 and 4 of the above linked file. The results show that the model is more prone to hallucinate on Attribute and Relationship conflicts than Object conflicts. Chain-of-Thought prompting baselines are also implemented and compared with our proposed methods, as shown in the linked file.
---
***We sincerely appreciate your thoughtful feedback. If our responses have adequately addressed your concerns, we would be grateful if you could consider raising your score. Thank you once again for your time and effort in reviewing our work.*** | Summary: This paper examines hallucinations in multimodal large language models (MLLMs) by focusing on "modality conflict" - inherent conflicts between different input modalities that create dilemmas for models. The researchers created a dedicated dataset called Multimodal Modality Conflict (MMMC) and evaluated three mitigation approaches: prompt engineering, supervised fine-tuning, and reinforcement learning. Their experiments showed that reinforcement learning performed best at reducing hallucinations caused by modality conflicts, while supervised fine-tuning demonstrated consistent and reliable results. This work highlights an overlooked cause of hallucinations and contributes insights into MLLM robustness.
Claims And Evidence: This paper introduces a research question called "modality conflict", and tries to address the question by building a dataset named Multimodal Modality Conflict (MMMC) and evaluates several baseline methods. Overall, I buy the idea.
Methods And Evaluation Criteria: This paper proposes a new setting and runs different baselines, which makes sense for the application at hand.
Theoretical Claims: There are no theoretical claims in this paper.
Experimental Designs Or Analyses: The experimental designs are reasonable and can convey interesting findings to readers.
Supplementary Material: I did not review the supplementary material.
Relation To Broader Scientific Literature: This paper is related to Multimodal LLMs.
Essential References Not Discussed: None
Other Strengths And Weaknesses: Strengths:
1. The paper proposes a reasonable setting as shown in figure 1.
2. The authors construct a new dataset called Multimodal Modality Conflict (MMMC) to study the proposed setting.
3. The authors run different baseline methods on this task and find reinforcement learning method achieves the best performance in mitigating the hallucination under modality conflict, while the supervised fine-tuning method shows promising and stable performance. MMMC obtains 20K image-question-answer triples.
Weaknesses:
1. Some visualization of the proposed dataset is needed so that readers can quickly know the data distribution of the dataset.
2. Which LLM did the authors use as Judge? Is it aligned to human evaluation? How about the evaluation results of different open-weight LLM and commercial LLM such as GPT-4o and Claude?
Other Comments Or Suggestions: None
Questions For Authors: Please see the weaknesses.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are delightful to see your positive remarks on our proposed research topic and experimental designs. We provide discussions about your suggestions as follows. All related results are available at the anonymous link [https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305](https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305).
**1. Some visualization of the proposed dataset is needed so that readers can quickly know the data distribution of the dataset.**
We have plotted the distribution of conflict types, and word clouds for text of each type, shown in Figure 1 and 2 of the above linked file. We will supplement these visualizations in the updated manuscripts.
**2. Which LLM did the authors use as Judge? Is it aligned to human evaluation? How about the evaluation results of different open-weight LLM and commercial LLM such as GPT-4o and Claude?**
We use GPT-4o-mini for Hallu-Rate and GPT-4o for LLM-Judge. These choices are based on the capacity of the models and the budget of the project. Both models are demonstrated to be well-aligned with human evaluation [1] and widely used in the community [2,3]. Since the judgement of Hallu-Rate is a binary classification task, GPT-4o-mini is enough to provide a reliable evaluation while saving computational resources. Judgement of LLM-Judge is a more fine-grained task, and GPT-4o is more suitable for this task.
To address your concerns, we also evaluate the results using an open-weight LLM, Llama-3.3-70B-Instruct. The evaluation results, shown in Table 5 of the above linked file, illustrate consistent conclusions with GPT-4o-mini and GPT-4o. We will include these results in the updated manuscript.
[1] Zheng, L., Chiang, W.-L., Sheng, Y., Zhuang, S., Wu, Z., Zhuang, Y., Lin, Z., Li, Z., Li, D., Xing, E. P., Zhang, H., Gonzalez, J. E., and Stoica, I. Judging LLM-as-a-Judge with MT-Bench and Chatbot Arena. In *Advances in Neural Information Processing Systems Track on Datasets and Benchmarks*. Curran Associates, Inc., 2023.
[2] Guan, T., Liu, F., Wu, X., Xian, R., Li, Z., Liu, X., Wang, X., Chen, L., Huang, F., Yacoob, Y., Manocha, D., and Zhou, T. HallusionBench: An advanced diagnostic suite for entangled language hallucination and visual illusion in large vision-language models. In *Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition*. IEEE, 2024.
[3] Yu, W., Yang, Z., Li, L., Wang, J., Lin, K., Liu, Z., Wang, X., and Wang, L. MM-Vet: Evaluating large multimodal models for integrated capabilities. In *Proceedings of the International Conference on Machine Learning*, 2024. | Summary: The paper investigates modality conflicts, which are the hallucination issues that are presented when the text and visual information are inconsistent. The paper defines modality conflict in terms of objects, attributes, and relationships, and constructs a Multimodal Modality Conflict (MMMC) dataset to evaluate MLLMs under these conditions. The authors also have explored using prompt engineering (PE), supervised training (SFT), and reinforcement learning (RL) to learn from the dataset. The results on three models (InstructBLIP, LLaVA-Next, and Qwen2) demonstrate that RL works the best in the end.
**Update after rebuttal**: My latest reply reflected my final update.
Claims And Evidence: 1. The paper proposes the MMMC dataset and provides experiments on multiple models (InstructBLIP, LLaVA-Next, and Qwen2).
2. The paper shows that RL generally performs better than PE and SFT in the MMMC benchmark, but SFT demonstrates less alignment tax.
[Weakness]
1. In lines 302 - 303, the paper mentions "Prompt engineering on Qwen2-VL-Instruct series brings significant improvement", but PE doesn't work well on the Qwen2-2B model as the Hallu-Rate increases.
Methods And Evaluation Criteria: * The datasets (MME, MMBench, AI2D, ...), models, and metrics (ROUGE, Hallu-Rate) are reasonable for evaluation.
Theoretical Claims: No Theoretical claims.
Experimental Designs Or Analyses: [Weakness]
* Given the instability of the approaches, particularly for RL, it would be beneficial to report averaged results across multiple seeds for each method to ensure robustness.
* The MMMC dataset consists of Object, Attribute, and Relationship Conflicts, yet the paper does not provide separate performance analyses for each category. Reporting these results would offer deeper insights into how well each approach handles different types of conflicts.
* A more rigorous evaluation, particularly on unseen domains, would strengthen the study. The construction of the current test set split is unclear, but to properly assess robustness, it should include samples with novel images, objects, attributes, and relationships to evaluate generalization beyond the training data.
* The paper would benefit from a broader set of baselines for hallucination mitigation, such as decoding-based methods for comparison.
Supplementary Material: No Supplementary Material.
Relation To Broader Scientific Literature: * The paper focuses on the conflicts between the modalities while previous work focuses on the conflicts between input and output, however, I thought the modality conflict was a special case of the later scenarios, as the hallucinated generation would also conflict with the inputs (e.g., images).
Essential References Not Discussed: I wasn't aware of any, but I am not an expert in this area so I might miss some references.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: * Since the paper mainly focuses on hallucinations, the second paragraph of Sec 5.1 can be a standalone section titled "Hallucinations in MLLMs".
* The numbers, scales, and range intervals will be more clear if changing Figure 3 to a table.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate your insightful comments and suggestions. We give a point-by-point response to each of your concerns below. Following the ICML 2025 Peer Review FAQ, we post all additional results to the anonymous link: [https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305](https://anonymous.4open.science/api/repo/11639-F609/file/Additional_Results.pdf?v=59a00305) for your reference.
**1. In lines 302 - 303, the paper mentions "Prompt engineering on Qwen2-VL-Instruct series brings significant improvement", but PE doesn't work well on the Qwen2-2B model as the Hallu-Rate increases**
We are sorry for the inaccurate description, and we will rewrite the claim as "Prompt engineering brings significant improvement to Qwen2-VL-Instruct-7B, but increases the Hallu-Rate of smaller Qwen2-VL-Instruct-2B model.". And we will carefully check the results and revise the manuscript accordingly.
**2. Given the instability of the approaches, particularly for RL, it would be beneficial to report averaged results across multiple seeds for each method to ensure robustness.**
We have rerun our SFT and RL approach across all models across three different seeds and computed the mean and standard derivation of these results, shown in Table 1, 2, 3 and 4 of the above linked file. The averaged results demonstrate consistent conclusions with the original results. We will include these results in the updated manuscript and carefully review the results to ensure the robustness of our findings.
**3. The MMMC dataset consists of Object, Attribute, and Relationship Conflicts, yet the paper does not provide separate performance analyses for each category. Reporting these results would offer deeper insights into how well each approach handles different types of conflicts.**
We analyzed the performance of each approach on Object, Attribute, and Relationship conflicts separately, as shown in Table 2, 3 and 4 of the above linked file. We find that results on each separate conflict types lead to similar conclusions as the overall results. However, MLLMs seem to be more prone to hallucinate on Attribute and Relationship than Object conflicts. This phenomenon may be due to the unbalanced training data distribution, as shown in Figure 1 of the above linked file, or the more abstract nature of Attributes and Relationships. We will include these results and related discussions in the updated manuscript.
**4. A more rigorous evaluation, particularly on unseen domains, would strengthen the study. The construction of the current test set split is unclear, but to properly assess robustness, it should include samples with novel images, objects, attributes, and relationships to evaluate generalization beyond the training data.**
We split the training and test set based on the image source, ensuring that the test set contains unseen images. Due to the multi-modal input nature of this task, we consider a input image-text pair as a unseen sample if either the image or the text is unseen. And thus the evaluation setting is able to reflect the generalization ability of the model. We will clarify this in the revised manuscript.
**5. The paper would benefit from a broader set of baselines for hallucination mitigation, such as decoding-based methods for comparison.**
We experimented with a strong decoding-based baseline, SID [1]. To ensure the correctness of our implementation, we run the original code provided by the authors of SID and test on LLaVA-v1.5-7B and InstructBLIP-7B. We also implement methods in our paper on the same models for comparison. The results, as shown in Table 1 of above linked file, indicate that the decoding-based SID gains comparable performance with prompt engineering baselines. We will include these results and discussions in the updated manuscript.
[1] Huo, F., Xu, W., Zhang, Z., Wang, H., Chen, Z., and Zhao, P. Self-Introspective Decoding: Alleviating Hallucinations for Large Vision-Language Models. In *Proceedings of the International Conference on Learning Representations*, 2025.
**6. Relation To Broader Scientific Literature**
We argue that modality conflict is a cause, rather than a special case of the later scenarios. In other words, we propose the concept of modality conflict to illustrate a source of hallucination, rather than describe the hallucination itself as previous works do. We will clarify this in the revised manuscript.
**7. Other Comments Or Suggestions**
Thank you again for these valuable suggestions. We will separate second paragraph of Sec 5.1 as a standalone section titled "Hallucinations in MLLMs" and convert Figure 3 to a table in the updated manuscript.
---
***We sincerely appreciate your thoughtful feedback. If our responses have adequately addressed your concerns, we would be grateful if you could consider raising your score. Thank you once again for your time and effort in reviewing our work.***
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the rebuttal contents, which have adequately addressed my concerns on evaluation. Thus, I have increased my rating.
---
Reply to Comment 1.1.1:
Comment: Thank you once again for increasing the rating. We greatly appreciate your insightful comments and will incorporate all of your suggestions into the revised manuscript. | null | null | null | null | null | null |
Learning Distances from Data with Normalizing Flows and Score Matching | Accept (poster) | Summary: The article proposes and compares several methods for estimating distances derived from Riemannian metrics that reflect the data distribution. In particular, the chosen metric should "compress" distances in regions of high mass concentration and "stretch" distances where the mass is lower. To achieve this, the authors consider conformal metrics (i.e., proportional to the identity) that are inversely proportional to the density of the underlying distribution of the observations. At a point $x$, the density-based metric is given by $\frac{I_d}{p(x)^{\frac{2}{d}}}$ where $p$ is the density of the observations and $d$ is the dimension of the space. Given a dataset where the density is unknown, the challenge is to estimate density-based distances and geodesics.
The authors propose two methods for estimating a density-based geodesic between any two points:
1) The first method relies on numerically solving (through relaxation) the differential equation whose solutions are geodesics. The authors provide an expression for this equation in the case of the density-based metric, which explicitly involves the derivative of the density. There are two approaches to estimate this quantity:
- Computing the derivative of the density numerically, where the density itself is estimated from the data using a normalizing flow.
- Directly estimating the density derivative using score matching—a method ultimately chosen because it is more efficient.
2) The second method approximates a density-based geodesic by finding the shortest path in a graph where edge weights are proportional to the density-based distance. This distance can be determined in two ways:
- Using the method of Bijarl et al. (2012), which estimates the density-based distance as a power of the Euclidean distance. However, the numerical simulations conducted by the authors do not yield good results with this technique.
- Estimating the density using a normalizing flow and then plugging it into the density-based metric expression.
For each of these two methods, the algorithm is detailed in the paper (Although I don't think they are new in the literature). To improve the numerical stability of the relaxation method, geodesics are parametrized to have constant Euclidean speed rather than constant speed relatively to the density-based metric.
The performance of a method is measured using the log of the ratio between the estimated distance and the true distance (log path ratio). Experiments are conducted on five datasets sampled from probability distributions with known densities (and thus known density-based metrics and distances). Several observations are made :
- The accuracy of density estimation is crucial for the precision of graph-based method.
- The relaxation method is much more accurate when the density derivative is estimated directly using score matching.
- As the dimension increases, the graph-based method suffers from the curse of dimensionality, whereas the relaxation method maintains good performance in high dimensions.
Given these observations, the authors recommend using the graph-based method to initialize the relaxation method.
## update after rebuttal
I thank the authors for their responses and clarification. The modifications announced by the authors seem reasonable and will help clarify the theoretical context of the paper. The topic of the paper, as well as the algorithms proposed by the authors, appear very interesting to me, although the experiments seem insufficient (especially considering that no theoretical guarantees are provided).
Claims And Evidence: The claims are based on a comparison of methods through experiments. Each performance value is obtained by averaging the log path ratio over 1000 pairs of points selected uniformly at random.
For the graph-based method, the performance of the two density estimation methods is compared using estimations on five datasets sampled from five different distributions in $R^2$. For the normal distribution only, a comparison is made between the graph-based method and the relaxation method as a function of the dimension.
The authors claim to have highlighted a gap between theory and practice, since their numerical estimates do not achieve the performance guaranteed by the results of Hwang et al. (2016), published in The Annals of Applied Probability. They speculate that the unknown constant in Hwang et al.'s result is responsible for this discrepancy.
It would have been interesting to discuss to what extent the assumptions of Hwang et al.'s result are satisfied in the case of the distributions used in the experiments.
Methods And Evaluation Criteria: See the paragraph above
Theoretical Claims: The theoretical claims consist in the development of the geodesic equation for the case of conformal metrics (i.e., proportional to the identity). These equations are provided first with constant speed relative to the density-based metric, and then relative to the Euclidean distance. The proof involves computing the Christoffel symbols and is provided in the appendix.
Experimental Designs Or Analyses: The experimental methodology is detailed in the appendix. The two deep learning models (normalizing flow and score matching) are trained on a training set (of unknown size), and the retained parameters are those that minimize the loss on the training set.
The experimental results are presented as the average of the performance metric over 1000 realizations. No additional indicators are provided (in particular, no empirical standard deviations).
Supplementary Material: Yes, the calculations as well as the details of the experimental methodology. The derivations are complete and clear.
Relation To Broader Scientific Literature: The algorithms used by the authors are already present in the literature. The authors suggest using deep learning methods to improve the performance of these algorithms by estimating quantities that are then plugged into the existing methods.
The approximation of geodesics by the shortest path in a graph, where edge weights depend on the density, was developed by Bijral et al. (2012). Dijkstra’s algorithm (1956) is used to compute the actual shortest path once the edge weights are determined. The authors suggest using a normalizing flow method to compute these weights instead of the approach by Bijral et al. (2012).
The approximation of geodesics by computing an approximate solution to the geodesic equation is likely already present in the literature, although no citation is provided in the paper. To improve numerical stability in computing an approximate solution to the geodesic equation, the authors seek a solution to the reparametrized equation so that the geodesic has constant Euclidean speed. Additionally, they propose using a score matching method to estimate one of the parameters of the geodesic equation (the gradient of the density).
The deep learning methods (normalizing flow and score matching) are well-referenced in the article.
Essential References Not Discussed: References that allow for the contextualization of the results are cited.
Other Strengths And Weaknesses: I am having trouble understanding the given definition of the metric tensor, particularly the sentence: "The metric tensor g is a smoothly varying positive-definite bilinear form on the tangent space." Does $g$ refer to a metric tensor field ($g: \ M \rightarrow TM$), which is a continuous function, or does it represent $g = g_p = g(p)$, the inner product defined on $T_p$ for $p \in M$? In the latter case, it would be more accurate to write $g_p$ and then $∣∣v∣∣_p=g_p(v,v)$ at the beginning of the following paragraph.
More generally, I am struggling to understand in which space the analysis in the paper is conducted. Section 2.1 suggests that it applies to an arbitrary smooth manifold equipped with a Riemannian metric. If that is the case, what does the probability density $p$ introduced on line 139 correspond to (density with respect to which measure, the Riemannian volume measure?) Similarly, does the change of variable formula (line 255) remain valid for random variables taking values in an arbitrary smooth manifold, where the considered measure is not the Lebesgue measure? Perhaps these objects are commonly used in Riemannian geometry for certain well-characterized spaces, but they should probably be justified more explicitly for readers who are not specialists in the field.
In Algorithm 1 (lines 282–284), you sum two elements of the space—what does this mean if the space is, for example, the sphere?
Given these remarks, perhaps your analysis is only intended to be valid in $R^n$ equipped with a Riemannian metric. If that is the case, I believe the introduction to Riemannian manifolds is unnecessary and could be replaced with the definition of a Riemannian metric on $R^n$ (without having to introduce the notion of tangent spaces).
Other Comments Or Suggestions: 1) L.109 column 2: Does “define distance between points in a distribution” mean “define distance between points sampled from a distribution”?
2) L.130 column 2: The first paragraph of “Fermat distances which scales with dimension” is written twice.
3) L.195 column 1: Equation (3) is true for geodesic trajectory so the sentence before is supposed to be “for a geodesic trajectory $\gamma$ we have”
Questions For Authors: Do you know in which Riemannian manifold the geodesics are always distance minimizers? (and so the geodesic equation (Eq. (3), line 197) has as solutions only geodesics that minimize distance). For example, this is not true in the sphere equipped with its usual metric, but perhaps it holds in $R^n$ with a conformal metric (it is true for the identity metric, and maybe conformality preserves this property?).
If this is not the case, perhaps initializing with the weighted graph method would help the relaxation method converge toward a distance-minimizing geodesic (since the weighted graph method is based on finding the shortest path rather than a on criterion related to the acceleration of the trajectory).
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Rebuttal to Reviewer nn54
We thank the reviewer for their careful and detailed reading of our work, and for the helpful questions and clarifications.
---
### Novelty of the Algorithms
> The algorithms used by the authors are already present in the literature.
While the Fermat distance itself is not a novel concept, our algorithms for computing it are, to our knowledge, new. In particular, Algorithm 1 introduces a reparameterization of the geodesic equation that ensures constant Euclidean speed along the curve, making the relaxation tractable and numerically stable. This reparameterization is key to our ability to exactly solve for geodesics in the Fermat metric — a setting where prior work has only used approximations.
Algorithm 2 also includes novel elements. While graph-based shortest paths are standard, our method departs from previous approaches that rely on Euclidean distances or kernel density estimates to define edge weights. Instead, we use edge weights derived from a learned density model, allowing for more accurate adaptation to complex, high-dimensional data. To our knowledge, this specific use of learned density-driven edge weights in computing Fermat distances has not been explored in the literature.
---
### Metric Tensor Notation
> Does $g$ refer to a metric tensor field ($g: M \to TM$), which is a continuous function, or does it represent $g = g_p = g(p)$, the inner product defined on $T_p$ for $p \in M$?
It is the latter. We will update the notation to make this clear and avoid confusion. Specifically, we will clarify that $g_p$ is a smoothly varying inner product on each tangent space $T_p$.
---
### Scope of the Analysis and Manifold Assumptions
> More generally, I am struggling to understand in which space the analysis in the paper is conducted.
We apologize for the confusion. You are correct — the analysis is conducted entirely in $\mathbb{R}^D$ equipped with a conformal Riemannian metric. We do not work on general manifolds. Thank you for pointing out that our use of manifold terminology in Section 2.1 may suggest otherwise. We will revise the exposition to streamline the definitions and make it explicit that our setting is $\mathbb{R}^D$.
---
### Clarification on “Distance Between Points in a Distribution”
> Does ‘define distance between points in a distribution’ mean ‘define distance between points sampled from a distribution’?
Yes, that is correct. Thank you — we will update the phrasing accordingly to avoid ambiguity.
---
### When Are Geodesics Distance-Minimizing?
> Do you know in which Riemannian manifold the geodesics are always distance minimizers?
This is indeed a challenging problem, and in general there are cases where multiple geodesics exist between two points, some of which are only local minimizers of the path length. For instance, in the case of the circle distribution (see Fig. 7), the shortest geodesic between two nearby points will traverse a small arc, but there is always another valid geodesic that takes the longer path around the circle. If the relaxation algorithm is poorly initialized, it may converge to such a non-minimizing solution. For this reason, we emphasize the importance of using a graph-based shortest path to provide a good initialization. This is described in Section 3.3 (line 289, column 2).
---
We appreciate the reviewer's in-depth engagement with the technical aspects of the paper and will incorporate the suggested clarifications to improve accessibility and precision. | Summary: The paper presents a method to learn distances from data by integrating normalizing flows and score matching into the computation of density-based distances (DBDs), specifically Fermat distances. It addresses the shortcomings of existing methods by introducing a stable numerical approach to compute true geodesics through normalizing flows and enhancing the smoothness of trajectories in high dimensions using score matching. The authors validate their approach by demonstrating faster convergence and improved accuracy over traditional graph-based methods, particularly in complex Gaussian mixtures and higher-dimensional spaces.
Claims And Evidence: The claims in the paper are supported by a mix of theoretical development and experimental results. The authors present a clear improvement in the accuracy and computational feasibility of estimating Fermat distances using their method. However, the claim regarding the general applicability of their approach in "real-world, high-dimensional applications" could be seen as overly optimistic, given the experiments are primarily on synthetic or simplified datasets. More evidence from diverse and complex real-world datasets would strengthen this claim.
Methods And Evaluation Criteria: The methods proposed, including the use of normalizing flows for accurate density estimation and score matching for refining geodesics, are well-suited to the stated problem of improving the computation of DBDs in high-dimensional spaces. The evaluation criteria, particularly the use of Log Path Ratio (LPR) for comparing different methods, is relevant and provides a clear metric for assessing improvements over existing approaches.
Theoretical Claims: The paper outlines several theorems related to the geodesic equations and their solutions using the proposed methods. The derivation of these theorems, such as the constant Euclidean speed parameterization and its impact on the stability of numerical methods, appears logically sound. No specific issues were identified in the proofs provided, but a more detailed external validation of these theoretical claims would ensure their robustness.
Experimental Designs Or Analyses: The experimental design seems valid for demonstrating the advantages of the proposed methods over traditional approaches. The use of synthetic datasets, while controlled, is appropriate for illustrating the performance improvements in known environments. The methodological setup, including comparisons to ground truth geodesics and other baseline methods, allows for a clear demonstration of the proposed method's superiority in terms of convergence rates and accuracy. However, expanding the experiments to include a broader range of real-world datasets would help validate the practical applicability of the methods outside controlled experimental conditions.
Supplementary Material: No, just looked at the figures
Relation To Broader Scientific Literature: The key contributions of the paper, specifically the integration of normalizing flows and score matching into the computation of density-based distances, draw significantly from the established fields of geometric deep learning and statistical machine learning. Prior research in normalizing flows has typically focused on improving the accuracy and efficiency of probability density function estimation in complex data distributions (e.g., Rezende and Mohamed, 2015). The application of these flows to compute Fermat distances introduces a novel intersection of geometric learning with probabilistic modeling, expanding upon works like those by Arjovsky et al. (2017) in Wasserstein GANs that explore distance metrics in latent spaces. The use of score matching, introduced by Hyvärinen (2005), for smoothing trajectory calculations in high-dimensional spaces further builds on the idea of refining probabilistic estimations without explicit density estimations.
Essential References Not Discussed: Beneficial not essential
While the paper adequately cites foundational works on normalizing flows and score matching, it may lack references to some pertinent studies that bridge these concepts more directly with geometric applications in machine learning. For instance, research by Bronstein et al. (2017) on geometric deep learning frameworks could provide additional context for the application of geometric principles in learning tasks. Additionally, recent advancements in computational geometry for machine learning, such as those presented in the works by Memoli (2011) on Gromov-Wasserstein distances, could enhance the theoretical underpinnings and practical applications of the methods discussed in this work.
Other Strengths And Weaknesses: Strengths:
Originality: The paper's approach to integrating normalizing flows with score matching to compute Fermat distances is highly original. This creative combination of techniques from different areas of machine learning could set a new precedent in the field.
Significance: The potential impact of this method in improving the computational feasibility and accuracy of distance calculations in high-dimensional spaces is significant, especially for applications in complex data analysis and geometric learning.
Clarity: The paper is well-written, with clear explanations of the methods and their theoretical foundations, making complex concepts accessible to readers.
Weaknesses:
Generalizability: The paper primarily demonstrates results on synthetic datasets. The generalizability of the approach to real-world datasets and its performance in truly unstructured environments remain to be validated.
Complexity Discussion: The computational complexity and resource demands of the proposed methods are not thoroughly discussed, which could be crucial for practical applications needing scalability considerations.
Other Comments Or Suggestions: I really liked Figure 1; it offers immediate clarity and a high level overview of your work.
While reviewing the paper, I noticed a few minor typographical errors that could be corrected to enhance the overall readability and professionalism of the manuscript:
On page 3, second paragraph, "theorm" should be corrected to "theorem."
On page 5, in Figure 2's caption, "illustraiting" should be changed to "illustrating."
It would also be beneficial to include a supplementary section with additional details on the parameter settings for the normalizing flows and score matching algorithms used in the experiments. This addition would aid in replicating the results and understanding the sensitivity of the proposed method to different configurations.
Questions For Authors: 1. Given that the paper primarily focuses on synthetic datasets, can you provide insights or preliminary results on how the proposed method performs on real-world datasets, particularly those with noise and irregular distributions?
2. Could you elaborate on the computational efficiency of your method, especially in comparison to traditional graph-based methods? What are the traditional graph-based methods that you may choose as a baseline? Specifically, what are the computational costs in terms of time and resources when applied to larger datasets?
3. Are there any specific assumptions or conditions under which the proposed theorems hold? How do these assumptions affect the generalizability of your findings?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## Rebuttal to Reviewer XLew
Thank you for your positive assessment of our work and for your thoughtful suggestions.
---
### Preliminary Results on Real-World Dataset
Please see our response to reviewer AqTp for a preliminary experiment on MNIST. We find that the distances obtained with our method behave as expected, and yield interesting insights into the relationships between the different classes.
---
### Computational Efficiency Compared to Graph-Based Methods
Please see the detailed discussion in our response to Reviewer EAyN. In short, the relaxation method (Algorithm 1) has per-iteration complexity that scales linearly with dimension due to the need to compute norms and inner products. The number of segments needed depends more on the complexity of the data than on the ambient dimension.
Graph-based methods similarly scale linearly with dimension in terms of distance computations, but their performance degrades significantly in higher dimensions, as shown in Figure 6, due to the sparsity of samples and the limitations of nearest-neighbor approximations.
---
### Assumptions Underlying Theoretical Results
The theorems provided in the paper, particularly the derivation of the geodesic equations and their reparameterization, rely on standard smoothness assumptions:
- The density function $p(x)$ is assumed to be differentiable and non-zero in the region of interest.
- The score function $s(x) = \nabla \log p(x)$ is assumed to be Lipschitz continuous.
- The conformal metric defined by $p(x)$ is smooth.
These conditions ensure the existence of solutions to the geodesic equations and support the stability of the relaxation method. They are commonly satisfied in practice, particularly when using neural networks for score estimation.
---
Thank you again for your encouraging review and support. | Summary: This paper addresses the problem of learning distance metrics from data, specifically focusing on density-based distances (DBDs). The authors highlight that existing methods for estimating Fermat distances suffer from poor convergence and scaling issues in high dimensions due to inaccurate density estimates and insufficiently smooth geodesics. To tackle these challenges, the paper introduces two main improvements: using normalizing flows to learn more accurate densities and refining geodesics with a learned score model. Additionally, the authors propose a dimension-adapted Fermat distance to improve scaling and numerical stability in higher dimensions. The core idea is to leverage density/score estimation using modern deep learning to improve the practical applicability of density-based distances.
## update after rebuttal
My questions and concerns have been addressed and I would be very happy to see the paper accepted.
Claims And Evidence: The claims made in the submission are generally well-supported by clear and convincing evidence. The authors provide both theoretical grounding and empirical results to back up their contributions.
* One key claim is that previous graph-based methods exhibit poor convergence. This is supported by the experimental results in Section 4.1.1 and Figure 5, which show that the power-weighted graph method converges slowly.
* The claim that normalizing flows improve density estimation is supported by the improved convergence rates observed when using normalizing flows for edge weights (Section 4.1.3 and Figure 5).
* The effectiveness of score-based relaxation in higher dimensions is demonstrated in Section 4.2 and Figure 6, where the relaxation method maintains performance while graph-based methods degrade.
However, there still remains a large gap as most of the examples considered in this paper are of extremely simplistic distributions and lower dimensions (compared to realistic datasets used in most fields).
Methods And Evaluation Criteria: The datasets used appear rather simplistic and hand-crafted. For example, none of the datasets appear to have disconnected support.
LPR appears to be a good performance metric, but following other similar works, I would suggest also considering geodesics standard geodesic error and geodesic variation errors as in https://arxiv.org/pdf/2403.06612 (eqns 115, 116).
Theoretical Claims: I have checked the correctness of the proofs for the theoretical claims in appendix A1. The derivation of the geodesic equation in Theorem A.2 and the reparameterization in Theorem A.3 appear to be correct, with steps clearly laid out.
Experimental Designs Or Analyses: They appear sound.
Supplementary Material: Appendices A1 and C2 appear sound.
Relation To Broader Scientific Literature: The paper appears to miss the recent proposals for learning geometry from data using score models (https://arxiv.org/abs/2405.14780) and normalizing flows (https://arxiv.org/abs/2410.01950).
Essential References Not Discussed: see above.
Other Strengths And Weaknesses: * The paper in its current form does not seem to address the question of time complexity required - especially how it relates to the dimension scaling.
*
Other Comments Or Suggestions: * I would strongly suggest clearly separating which methods are graph based and which are not, as currently it is not clear at times.
and see below.
Questions For Authors: * Fermat Distance dimension scaling - the example provided makes a lot of sense when considering gaussian distributions. But it is unclear to me whether the same scaling should be used when considering a different distribution - could you comment/elaborate on validity in other cases?
* Line 133 - you mention that beta = 1 is common in previous works, which would be useful to have a couple of references for.
* Could you comment on how slow Algorithm 1 is? Also, if the initialization is not done using normalizing flows, is the geodesic still computed accurately?
* How is the true geodesics distance in (13) computed?
* Line 358 - when referring to supplementary materials, please provide where in supplemetaries this can be found.
* There appear to be no graphs for using normalizing flows directly for relaxation. Could you either point me to where they can be found or include them? You appear to claim that they are not very good and it would be good to understand what exactly you mean by that.
* Building on the previous question - NF trianed with maximizing likelihood would make sense to not be very good at approximating the score. Have you tried training an NF with a mix of likelihood and sliced score matching? It is not clear to me why both can be optimized for.
* Line 434 - what do you mean "Unifying nf and score models into a single framework?"
* Line 102 - you claim to "Introduce a numerically stable relaxation method" - what exactly do you mean by this? Is this your novel contribution?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## Rebuttal to Reviewer EAyN
We thank the reviewer for their detailed and constructive comments.
---
### Simplicity of Experiments
Please see our response to reviewer AqTp for results on an experiment on MNIST.
---
### Missing Recent Work
Thank you for pointing out our oversight. We will add both references to the discussion of related work.
---
### Time Complexity and Scaling
Scaling the dimension does not necessarily increase the number of segments needed in the relaxation algorithm — this depends on the complexity of the dataset (see also our response to Reviewer AqTp). The complexity per iteration of the loop scales linearly with dimension, due to norm and inner product computations. So overall, the complexity of relaxation is roughly linear in dimension.
For the simple case of a uniform distribution (where the score is zero and the solution is a straight line), we can show that convergence requires $O(n^2)$ iterations, where $n$ is the number of segments. While a full analysis in general cases is more challenging, we can provide this estimate as a starting point and are happy to add more details in the appendix if helpful.
The graph-based algorithms also scale linearly in dimension, but the number of nearest neighbors may need to increase with dimension to preserve local structure. However, as shown in Figure 6, graph-based methods degrade in high dimensions due to sparsity and noise, often before computational scaling becomes the limiting factor.
---
### Fermat Distance Scaling in Non-Gaussian Distributions
You are correct — our original discussion was overly focused on the Gaussian case. For a generalized Gaussian distribution of the form $p(x) \propto \exp(-\|x\|^\alpha / \alpha)$, it can be shown that $\mathbb{E}[\|x\|^\alpha] = D$, and thus the typical distance from the origin scales as $D^{1/\alpha}$. The score in this case is $s(x) = -\|x\|^{\alpha - 2} x$.
By rescaling $\gamma$ in Eq. (3) by $D^{1/\alpha}$, all terms in the equation scale consistently if and only if $\beta = 1/D$. The same reasoning applies to the reparameterized equation (Eq. (4)).
A similar argument can be made for the Student-t distribution, where $p(x) \propto \left(1 + \|x\|^2 / \nu\right)^{-(\nu + D)/2}$. The scaling is approximate in this case but still suggests that $\beta = 1/D$ is a natural default across a wide range of distributions.
Thank you for encouraging us to clarify and strengthen this argument — we will update the text and appendix accordingly.
---
### Speed and Initialization of Algorithm 1
Please see our earlier comments on time complexity. Regarding initialization: it is indeed possible to initialize the relaxation algorithm using simpler paths, such as power-weighted shortest paths based only on Euclidean distances. This often works well in practice and is especially useful when only the score is available (without a density model).
---
### Computation of Ground Truth Geodesic Distance (Eq. 13)
We use Algorithm 1 with the ground truth score function to compute true geodesics. Initial trajectories are obtained using a graph-based approximation. This is discussed in Section 3.1.
---
### Absence of Graphs for NF-Based Relaxation
You are right — we do not include plots of NF-based relaxation because the scores derived from differentiating normalizing flow models are quite noisy. This frequently causes the relaxation algorithm to diverge, making the results unreliable for evaluation. This is precisely why we trained separate score models.
---
### Hybrid Training of NFs with Score Matching
We experimented with combining maximum likelihood training and sliced score matching. Unfortunately, this either did not improve the quality of the scores or led to training instability. We are not certain of the root cause, but we suspect it reflects the trade-off between optimizing for density accuracy and gradient (score) accuracy — see the discussion in Appendix C.2.
---
### Line 434: Unifying Normalizing Flows and Score Models
By this, we mean developing a single model that yields both accurate densities and scores. Our attempts to do so with normalizing flows were not successful (see comment above), so we leave this as a challenge for future work.
---
### Line 102: Numerically Stable Relaxation Method
We refer here to our relaxation method based on a reparameterized geodesic equation, which enforces constant Euclidean speed. This improves numerical stability and simplifies discretization. To our knowledge, this reparameterization has not appeared in prior work and is a novel contribution of this paper.
---
We thank the reviewer again for their thoughtful feedback and for helping us sharpen the clarity and scope of the work. | Summary: In this paper, the authors propose to learn a Riemannian metric from data using a class of Fermat metrics, which are metrics that are equal to the Euclidean metric rescaled at each point by (a power of) the reciprocal of the probability density of the data. This way, geodesics tend to follow high density regions, which is desirable e.g. to interpolate between data points. The authors point out limitations of current estimators of this type of distances, mostly because of poor density estimation and the curse of dimensionality. They introduce a relaxation scheme to numerically solve for geodesic segments linking two fixed endpoints when the ground truth density is known (this allows computing geodesics for known densities). They also modify existing graph based methods by estimating the density with normalizing flows. They finally introduce another method which combines the relaxation scheme with score estimation. The methods are tested on 2D examples whose ground truth densities are known, and the score based method is tested on higher dimensional standard Gaussians. The competing methods are the graph based methods that don’t use deep learning techniques for density estimation.
## Update after rebuttal
Thanks to the authors for the responses and the preliminary experiments on MNIST. I would indeed be nice to add an appendix to discuss these, though more extensive experiments and theoretical results would have strengthened the paper even more. I still have an overall positive opinion on this paper, so I will maintain my score.
Claims And Evidence: The paper makes a certain number of claims compared to the existing literature. First the capacity to use the relaxation algorithm for datasets with known densities enables quantitative comparisons, which were not extensively performed previously. This in particular can help show shortcomings of classical graph based methods in the experiments. The density estimation for graph based methods seems to be the issue, and indeed using NF for this purpose improves performance. The combination of the score estimation and the relaxation method seems to scale better with dimensionality(up to d = 30), albeit only a single experiment using standard normals is performed.
Of course, the claim of the score based method to scale well with dimensionality calls for experiments on e.g. image datasets. Score based methods are known to scale very well with dimensionality, so this raises two questions :
1) How large can the dimension become for the relaxation method to stay efficient and tractable? The finite difference scheme must require finer discretization in higher dimensions, I suppose? Maybe in that case the NF graph based method would be a better choice if there are sufficiently many samples?
2) How would the method perform in small and simple image datasets such as MNIST or CIFAR (possibly working in a latent space if the input dimension of the images turn out to be too large) ? I understand that in this case no GT density is available but qualitative behavior can be analyzed and it would be interesting to see shortest paths in image space.
Methods And Evaluation Criteria: Though I am not very familiar with the literature on learning Fermat metrics, the introduction of a method that allows to compute ‘GT’ geodesics for known densities is definitely a good thing for the domain if it was hard to compare to true geodesics before. It apparently helped identifying shortcomings of previous classical methods, in spite of apparently reassuring theoretical guarantees.
Theoretical Claims: I checked the proofs and derivations. I assume the geodesic equation for Fermat metrics is a known result (reference?) and that only the reparameterization is new. This should be precised in the text.
Is there an existing result on the convergence of the relaxation scheme (when successive values become closer and closer) ? This seems like an important result to have to further strengthen the method. Similarly, investigating further the reason why convergence of the classical graph based method is so low in practice would be interesting.
Experimental Designs Or Analyses: The experiments are sound and show the improvements brought by the two methods that introduced. The remarks on the difficulty of estimating the density and its score simultaneously are interesting and are somewhat reminiscent of Heisenberg’s uncertainty principle.
Supplementary Material: I reviewed all the appendices.
Relation To Broader Scientific Literature: I am not an expert on Fermat metric learning, so I cannot comment on the exhaustivity of the related work on methods for this. However, the paper is clearly positioned among the papers that are cited.
Essential References Not Discussed: No missing references to my knowledge.
Other Strengths And Weaknesses: - The lack of experiments in higher dimensions is a bit of a shame, as it would really tell about the potential of the method for generic ML tasks and datasets.
- I suggest adding a plot showing an example of geodesics recovered on a dataset by the different methods. Something similar to Figure 4, but not restricted to graph based methods.
- In line with my comment on the convergence of the relaxation scheme, a plot with approximated geodesics with various discretization levels would be interesting (how is this chosen in practice?).
Overall the paper is interesting with a number of compelling elements, but it feels slightly limited in terms of theoretical guarantees and experiments on higher dimensional datasets would be most welcome.
Other Comments Or Suggestions: - Figs 1 and 4 are not referenced in the text.
- There is a repeated sentence in p3, right column, below Fig. 2.
- I suggest setting the same extent on the y axes of both plots for each columns of Fig. 10 for better comparison between both cases.
Questions For Authors: See my questions the boxes above.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: ## Rebuttal to Reviewer AqTp
We thank the reviewer for their thoughtful and constructive feedback. Below, we address each of the main points and questions raised.
---
### How large can the dimension become for the relaxation method to stay efficient and tractable? The finite difference scheme must require finer discretization in higher dimensions, I suppose?
The tractability of the relaxation method primarily depends on the complexity of the data, rather than the ambient dimension. For example:
- Uniform distributions: Our method correctly converges to straight lines even with very coarse discretization.
- Standard normal: Reduces to the 2D case (due to rotational symmetry when using β = 1/D), and we find that 20 segments are sufficient for accurate geodesics, even in high dimensions.
More complex distributions may require finer discretization for accuracy, but there is no intrinsic limitation due to dimension itself. In contrast, the NF graph method becomes increasingly ineffective in higher dimensions, as filling the space requires exponentially more samples due to the curse of dimensionality.
---
### How would the method perform in small and simple image datasets such as MNIST or CIFAR?
We agree that applying the method to image data is an exciting next step. While ground truth densities are unavailable, qualitative insights (e.g., visualizing shortest paths) can still be informative.
As a first step, we train an autoencoder to compress MNIST to a 10-dimensional latent space, then train a normalizing flow and score model on the latent distribution. Solving for geodesics yields plausible digit interpolations.
As an initial quantitative measure, we report mean and standard deviation of log distances between each digit cluster mean and 200 random samples of the same or other digits:
| Digit | Same Class | Other Class | Diff (Other-Same) |
|-------|--------------------|--------------------|--------------------|
| 0 | 2.41 ± 0.40 | 3.73 ± 0.27 | 1.32 ± 0.49 |
| 1 | 1.69 ± 0.49 | 3.73 ± 0.31 | 2.04 ± 0.58 |
| 2 | 3.56 ± 0.29 | 4.05 ± 0.19 | 0.49 ± 0.35 |
| 3 | 3.03 ± 0.33 | 3.78 ± 0.24 | 0.75 ± 0.41 |
| 4 | 3.04 ± 0.38 | 3.77 ± 0.36 | 0.73 ± 0.53 |
| 5 | 3.43 ± 0.35 | 4.02 ± 0.18 | 0.59 ± 0.39 |
| 6 | 2.89 ± 0.41 | 3.79 ± 0.31 | 0.91 ± 0.51 |
| 7 | 2.86 ± 0.47 | 3.81 ± 0.30 | 0.95 ± 0.56 |
| 8 | 3.29 ± 0.33 | 3.74 ± 0.21 | 0.46 ± 0.39 |
| 9 | 2.76 ± 0.45 | 3.56 ± 0.38 | 0.80 ± 0.59 |
We see that same-class distances are always lower than other-class distances, up to a safe margin of error. We also note: 1s cluster tightly, likely due to fewer active pixels and therefore higher likelihoods; 8s are more ambiguous, likely due to easy deformations into other digits (it is quite easy to remove some pixels to turn an 8 into a 3, 5, 6 or 9). We will include these results and visualizations in the paper, but leave deeper analysis of Fermat distances on MNIST to future work.
---
### I assume the geodesic equation for Fermat metrics is a known result (reference?), and that only the reparameterization is new.
Yes, the form of the geodesic equation for conformal metrics follows from standard Riemannian geometry (e.g., see Appendix G of *Spacetime and Geometry*, Carroll, 2004). The reparameterization to constant Euclidean speed is indeed new and key to our numerically stable relaxation scheme.
---
### I suggest adding a plot showing an example of geodesics recovered on a dataset by the different methods.
Agreed—we will add such a figure to the main text to complement Figure 4, comparing several methods on the same dataset.
---
### A plot with approximated geodesics with various discretization levels would be interesting.
We will add such a figure to the appendix to illustrate convergence behavior and practical trade-offs.
---
### Minor Comments
- Figures 1 and 4: Will ensure they are clearly referenced.
- Repeated sentence on p3: Will be removed.
- Fig. 10: Will standardize y-axis ranges for better visual comparison.
---
We thank the reviewer again for their detailed review and insightful suggestions. We believe these improvements will significantly strengthen the clarity and impact of the paper. | null | null | null | null | null | null |
On the Vulnerability of Applying Retrieval-Augmented Generation within Knowledge-Intensive Application Domains | Accept (poster) | Summary: This paper investigates the vulnerabilities of retrieval systems to various poisoning attacks. The authors first analyze multiple corpora, retrievers, and datasets, highlighting the significant safety risks in retrieval. They then attribute retriever failures to the limitations of the existing document embedding distance metric. Finally, they propose a new metric that more effectively differentiates between clean and poisoned documents.
## update after rebuttal
Thank you for your response and the insightful experiments. The authors have addressed most of my concerns, and I have accordingly increased my original score.
Claims And Evidence: 1. The retrieval of safety risks in health and legal document retrieval systems includes detailed experiments, but the number of retrieved documents remains limited.
2. The observation that poisoned documents exhibit orthogonal augmentation with their corresponding clean queries is interesting.
3. The proposed new defense method is well-supported by evidence.
Methods And Evaluation Criteria: The proposed defense method and analysis of retrieval system vulnerabilities in RAG are reasonable. However, I believe the author could incorporate additional evaluation metrics, such as the MRR score, to enhance the assessment.
Theoretical Claims: There is no theoretical claim in paper.
Experimental Designs Or Analyses: 1. You should include additional retrieval cases to better demonstrate the effectiveness of your method, especially in the legal domain.
2. The paper uses only the l2-norm-based defense as a baseline for evaluating the proposed method. This baseline is relatively simple, making the comparison results less convincing.
3. Balancing performance and efficiency: While ensuring the effectiveness of the defense method, how can its application efficiency be improved for large-scale data and real-time systems? Is there room for further optimization to meet practical performance requirements?
4. Why not use cosine similarity? Have the results under cosine similarity been evaluated?
Supplementary Material: I reviewed all supplementary materials.
Relation To Broader Scientific Literature: It proposes a detection method to enhance the defense against attacks on RAG systems.
Essential References Not Discussed: There need more realted work for attack on RAG system, such as HijackRAG[Zhang'24], AgentPoison[Chen'24], BadRAG[Xu'24]
Other Strengths And Weaknesses: 1. The description of the defense is not clearly explained, easy to make confuse to reader.
2. How about top5, top10 retrieval performance
Other Comments Or Suggestions: There are no obvious typos.
Questions For Authors: The concept of orthogonal augmentation is intriguing, but it appears to be influenced by the principles of modern Hopfield networks. When the model’s query $q$ and the memory document
$p$ are orthogonal, the energy function is significantly lower, making knowledge retrieval more efficient. Could you provide a mathematical explanation for why orthogonal augmentation enhances retrieval? Is it because the target attack document embedding is injected into the original query $q$, thereby modifying its representation? This interpretation seems reasonable to me.
Ethical Review Flag: Flag this paper for an ethics review.
Ethics Expertise Needed: ['Privacy and Security']
Ethical Review Concerns: I would recommend adding a flag in the abstract to indicate potential harmful information. This would help in identifying and addressing any sensitive or risky content upfront, ensuring that readers are aware of it before diving deeper into the paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewers for investing their time and effort in reviewing our manuscript and providing valuable feedback. We will address their comments point by point in the following and incorporate them into our revision.
> Q: additional retrieval cases ..., especially in the legal domain.
**R**: We actually included the experiments on the legal domain in *Table 10 in Section D in the supplementary material*. Overall, we observe similar attack success rates in the legal domain as in the medical domain presented in the main text. We will highlight this in the revised version.
> Q: l2 norm baseline relatively simple
**R**: $\ell_2$-norm is a simple but also the standard baseline in many existing literature [1,2,3]. To address your concern, following [1,2,3], we also include the perplexity filter, which examines the perplexity of the text, as an additional baseline. The results are shown in the Table below where we observe that the perplexity filter is not effective, thus validating the effectiveness of our method.
Table: Detection rate of the perplexity filter on the MedMCQA corpus. The results are averaged over 5 runs.
| Datasets | MMLU-Med| MedQA | BioASQ|
|--------------------|---------------------|---------------------|---------------------|
| Detection Rates | 0.09 | 0.14| 0.16 |
> Q: application efficiency be improved for large-scale data and real-time systems?
**R**: We are not 100% certain regarding what you mean by "application efficiency." So we will refer to the computation cost/efficiency of our method and respond accordingly. The computation of our defense method is very light. We only need to compute the covariance **offline once**, and then during inference time, we only need to calculate the Mahalanobis distance **once** for each query, which is very efficient. To further improve efficiency, we can take a batch of queries and compute the Mahalanobis distance for all queries in the batch simultaneously.
> Q: cosine similarity
**R**: The use of inner product is a common practice in current literature [1,2,3]. To address your concern, we also evaluated cosine similarity and the summarized results are shown in the table below. We observe similar high attack success rates when using cosine similarity. We will include this in the revised version.
Table: Top 2 retrieval success rates under cosine similarity with Contriever as the retriever and MedMCQA, PubMedQA as the query corpus.
| Corpus | Attack Success Rate |
|--------------------|---------------------|
| Textbook | 0.95 |
| StatPearls | 0.94 |
| PubMed | 0.90 |
> Q: The description of the defense is not clearly explained, easy to make confuse to reader.
**R**: We will revise the description of the defense in the main text to make it clearer. The main workflow of our defense is for the defender to select a set of clean corpus (corresponding to a set of queries) to be protected. Then, the defender computes the covariance of the embeddings of the clean corpus. During inference time, for each query, the defender computes the Mahalanobis distance between the query and the clean corpus. If the distance is larger than a threshold, the query is rejected.
> Q: How about top5, top10 retrieval performance
**R**: The retrieval rates reported in the main text are a non-decreasing function of the $k$ value used in the retrieval. So the top-5 and top-10 retrieval performance will be no worse than the top-2 retrieval performance. In particular, we report the results for $k=10$, where we observe near perfect retrieval rates. We will include this in the revised version.
Table: Top-10 retrieval success rates with Contriever as the retriever and MedMCQA, PubMedQA as the query corpus.
| Corpus | Attack Success Rate |
|--------------------|---------------------|
| Textbook | 0.99 |
| StatPearls | 0.98 |
| PubMed | 0.94 |
> Q: More related work and flag in the abstract for potential harmful information
**R**: We will include more related work as you suggested. We will also add a flag in the abstract to indicate that the paper contains potentially harmful information.
> Q: Math explanation
Providing rigorous mathematical justification is challenging due to the sparse, preliminary theoretical understanding of transformer-based models [4]. We aim to address this in future work.
Refs:
[1] Xiong et al., "Benchmarking Retrieval-Augmented Generation for Medicine", ACL 2024
[2] Miao et al., "Integrating Retrieval-Augmented Generation with Large Language Models in Nephrology: Advancing Practical Applications", Medicina (Kaunas). 2024
[3] Zou et al., "PoisonedRAG: Knowledge Poisoning Attacks to Retrieval-Augmented Generation of Large Language Models", USENIX Security, 2025
[4] Tian et al., "Scan and Snap: Understanding Training Dynamics and Token Composition in 1-layer Transformer", NeurIPS 2023.
---
Rebuttal Comment 1.1:
Comment: Thank you for your response and the insightful experiments. The authors have addressed most of my concerns, and I have accordingly increased my original score.
---
Reply to Comment 1.1.1:
Comment: We are very pleased to have addressed your concerns and thank you very much for raising the score! | Summary: This paper focuses on the adversarial robustness of the retrieval system of RAG against data poisoning attacks.
Three major safety risks are discussed, including the leakage of PII, adversarial recommendations, and the vulnerability to jailbreaking attacks.
Extensive experiments on five Medical QA datasets demonstrate the prevalence of such risks, i.e., the retrieval systems used for medical QA are universally vulnerable.
This paper also discusses the possible reason for such risk and proposes a new defense to mitigate them.
Claims And Evidence: According to Section 1.1, the main claims include:
1. Revealing the safety risks for the retrieval system. Three safety risks are mentioned, including the leakage of PII, adversarial recommendations, and the vulnerability to jailbreaking attacks.
2. Providing an explanation for the vulnerability of retrieval system to data poisoning attacks.
3. Proposing a new defense method against universal poisoning attack.
All the claims are well supported by experiments.
Methods And Evaluation Criteria: The experimental results of this paper evaluate and reveal the safety risk of the existing retrieval systems. The methods and evaluation criteria make sense for the application.
Theoretical Claims: This paper does not provide theoretical analysis.
Experimental Designs Or Analyses: I have checked the soundness/validity of the experimental designs (regarding the main claim of this paper) in Section 3. My main concern is that the retrievers mentioned in Lines 185-192 (right) are slightly out-of-date.
Supplementary Material: I have reviewed Sections A and B of the supplementary materials. I believe Sections C and D are not directly related to the main contribution of this paper.
Relation To Broader Scientific Literature: Section 1.2 has comprehensively discussed the related study of this paper.
Essential References Not Discussed: I am not aware of such related works.
Other Strengths And Weaknesses: 1. This paper is well-organized and carefully written. The seemingly unrealistic assumptions are explained in the remarks. The preliminary section is very helpful for readers unfamiliar with the topic.
Other Comments Or Suggestions: 1. I suggest including more illustrative examples to further improve the presentation of this paper. The examples given in Figure 1 seem artificial. In Section A, some examples from the real dataset are presented. I suppose presenting some real-world examples can better illustrate the safety risk faced by the RAG systems.
Questions For Authors: 1. In Lines 105 (left) and 150 (right), the notation $f$ refers to the retrievers and the embedding function, respectively. Could the authors please provide some explanation regarding the definitions of the retrievers?
2. Besides, the results in Sections 3-5 heavily rely on the embedding function of the input. However, my past experience implies that the performance of those embedding models released before 2024, especially those token-level models like BERT, is far from satisfactory. As mentioned in the "Experimental Designs Or Analyses" part, I suppose the retrievers used in this paper are slightly out of date. (P.S. I am unfamiliar with RAG's research, and thus, I cannot provide extract references.) Are there any retrieval systems that are based on SOTA embedding models, e.g., text-embedding-3 from OpenAI?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewers for investing their time and effort in reviewing our manuscript and providing valuable feedback. We will address their comments point by point in the following and incorporate them into our revision.
>Q: In Lines 105 (left) and 150 (right), the notation refers to the retrievers and the embedding function, respectively. Could the authors please provide some explanation regarding the definitions of the retrievers?
**R**: In our paper, we use the terms "retriever" and "embedding function" interchangeably, which take an input text and output a vector representation of the text. We will clarify this point to avoid confusion in the revised version.
>Q: Besides, the results in Sections 3-5 heavily rely on the embedding function of the input. However, my past experience implies that the performance of those embedding models released before 2024, especially those token-level models like BERT, is far from satisfactory. As mentioned in the "Experimental Designs Or Analyses" part, I suppose the retrievers used in this paper are slightly out of date. (P.S. I am unfamiliar with RAG's research, and thus, I cannot provide exact references.) Are there any retrieval systems that are based on SOTA embedding models, e.g., text-embedding-3 from OpenAI?
**R**: The three retrievers used in the main text are the state-of-the-art models for RAG following very recent literature [1,2,3]. To address your concern, we also include the results of the text-embedding-3 from OpenAI in the Table below. We observe that the attack success rates are similar to those of the state-of-the-art models. We will include this in the revised version.
Table. Top 2 retrieval success rates with text-embedding-3 as the retriever and MedMCQA, PubMedQA as the query corpus.
| Corpus | Attack Success Rate |
|--------------------|---------------------|
| Textbook | 0.95 |
| StatPearls | 0.90 |
| PubMed | 0.83 |
>Q: I suggest including more illustrative examples to further improve the presentation of this paper. The examples given in Figure 1 seem artificial. In Section A, some examples from the real dataset are presented. I suppose presenting some real-world examples can better illustrate the safety risk faced by the RAG systems.
**R**: We will follow your suggestions to replace the current Figure 1 and include some real-world examples in the main text to better represent the safety risks faced by RAG systems.
Refs: [1] Xiong et al., "Benchmarking Retrieval-Augmented Generation for Medicine", ACL 2024
[2] Miao et al., "Integrating Retrieval-Augmented Generation with Large Language Models in Nephrology: Advancing Practical Applications", Medicina (Kaunas). 2024
[3] Zou et al., "PoisonedRAG: Knowledge Poisoning Attacks to Retrieval-Augmented Generation of Large Language Models", USENIX Security, 2025
---
Rebuttal Comment 1.1:
Comment: Thanks the authors for their reply. Most of my concerns are addressed. It is a surprising result that SOTA embedding model does not significantly affect the success rate. Could the authors explain the intuition behind this? | Summary: This paper explores a characteristic of poisoned documents in embedding spaces termed the orthogonal augmentation property. It suggests that appending target information to a poisoned document containing the target query shifts its embedding orthogonally to the query, preserving its retrievability by the query. The authors analyze how this property enables certain attacks and propose a corresponding defense.
Claims And Evidence: The claim that dense retrievers are vulnerable to universal poisoning attacks is well-supported by extensive experiments. The Orthogonal Augmentation Property claims are also backed by experiments, and the proposed defense is evaluated empirically. However, I have some concerns about the experimental results related to the Orthogonal Augmentation Property and the defense's effectiveness (see Weaknesses).
Methods And Evaluation Criteria: Yes
Theoretical Claims: N/A
Experimental Designs Or Analyses: The experiments on medical retrieval systems appear sound.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The paper tries to explain the success of poisoning attacks against RAG by analyzing the behavior of poisoned documents in dense retrieval embedding spaces and provides experimental insights. It also proposes a new defense against a specific type of such attack.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: ### Strengths:
1. Provides some insights into the behavior of poisoned documents in embedding spaces.
2. Conducts comprehensive experiments on different medical datasets and retrievers to evaluate the retrieval of poisoned documents.
### Weaknesses:
1. Universal poisoning attacks against RAG have already been shown to be effective [1]. The paper dedicates significant space to revalidating this on medical retrieval systems, which seems of limited value.
2. The orthogonal augmentation property essentially demonstrates a simple fact: a poisoned document containing the target query is naturally more retrievable than a clean document by the target query. The necessity of proving this through a convoluted approach is unclear.
3. The proposed defense requires access to a collection of clean documents and prior knowledge of the target queries, which is a strong assumption, making it impractical in real-world scenarios.
4. The paper focuses only on dense retrievers, leaving it unclear how the findings extend to models like ColBERT or retrieval architectures incorporating cross-encoder re-rankers, which are widely used.
[1] PoisonedRAG: Knowledge Corruption Attacks to Retrieval-Augmented Generation of Large Language Models, USENIX Security'25.
Other Comments Or Suggestions: N/A
Questions For Authors: 1. It is common practice to append potential queries to documents to improve retrievability, a technique also known as Doc2Query [1]. How would the findings of this paper and the proposed defense apply to retrieval systems that incorporate Doc2Query?
[1] Document expansion by query prediction, 2019.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewers for investing their time and effort in reviewing our manuscript and providing valuable feedback. We will address their comments point by point in the following and incorporate them into our revision.
>Q: Universal poisoning attacks against RAG have already been shown to be effective [1] ...
**R**: Thank you for your valuable suggestions regarding the work in [1]. Overall, our work differs from [1] in terms of goals, insights, and application scenarios, despite the similarity in attack implementations. Detailed discussions are provided as follows.
- **Goal**. Our objective is to investigate and comprehend the robustness of retrieval systems employed in RAG. We achieve this by injecting various types of information, encompassing both irrelevant and relevant content, into the corpus and evaluating the ease or difficulty of retrieval. The goal of [1], on the other hand, is to inject only query-relevant context to deceive the LLM's generation process upon retrieval.
- **Insights**. We provide explanations on the difficulty/easiness of the retrieval of different kinds of information, which is not covered in the work of [1]. Moreover, based on the developed insights, we propose a new defense that can effectively filter out the adversarial documents generated by [1].
>Q: The orthogonal augmentation property essentially demonstrates a simple fact ...
**R**: The `orthogonal augmentation` property concerns the effects on **changes in embedding vectors** generated by text embedding models when manipulating the text input. Specifically, `orthogonal augmentation` examines the relationship between $f(q)$ and the change in the embedding space that occurs when shifting
$q$ to $q \oplus p$, namely $v \triangleq f(q \oplus p) - f(q)$, for two documents $p$ and $q$, which can be either semantically relevant or irrelevant (as discussed in Section 4).
Overall, we feel that it is essential to understand the `orthogonal augmentation` property, as it can be seen in many poisoning attacks against text embedding models. We tried to investigate this property both in theoretical and empirical ways. It turns out the current literature on the theoretical understanding of transformer-based models seems to be sparse and preliminary. For example, recent research, such as the work [A] published in NeurIPS 2023, studied the weight dynamics of transformers under strong assumptions which may not align with real-world use cases, such as single-layer self-attention, no positional encoding, and excessively long input contexts. As a result, in the paper, we present the empirical study of the `orthogonal augmentation` property.
>Q: The proposed defense requires access to a collection of clean documents ...
**R**: We feel that the assumption is reasonable in the following sense. First, it is straightforward (and can be theoretically proven) to see that the defender is impossible to defend all corpus/queries (Because that would make the whole input space to be clean). As a result, a more feasible solution is to find a set of important queries and their corresponding corpus and then prioritize protecting these selected ones. In fact, many RAG poisoning attacks are targeted attacks in the sense that the attacker only wants to poison/manipulate a small set of queries [2,3,4]. So we believe that such an assumption is reasonable. We will clarify this in the revised version.
>Q: The paper focuses only on dense retrievers, leaving it unclear how the findings extend to models like ColBERT or retrieval architectures incorporating cross-encoder re-rankers ...
**R**: The MedCPT retriever used in our paper is actually of the cross-encoder re-rankers architecture tuned on medical data (https://github.com/ncbi/MedCPT). As a result, we think the observations and findings are applicable to the cross-encoder re-rankers. We also include the results of close-sourced text-embedding-3 from OpenAI in the Table below. We observe that the attack success rates are similar to those of the state-of-the-art models. We will include this in the revised version.
Table. Top 2 retrieval success rates with text-embedding-3 as the retriever and MedMCQA, PubMedQA as the query corpus.
| Corpus | Attack Success Rate |
|--------------------|---------------------|
| Textbook | 0.95 |
| StatPearls | 0.90 |
| PubMed | 0.83 |
Refs:
[A] Tian et al., "Scan and Snap: Understanding Training Dynamics and Token Composition in 1-layer Transformer", NeurIPS 2023.
[2] Xiong et al., "Benchmarking Retrieval-Augmented Generation for Medicine", ACL 2024
[3] Miao et al., "Integrating Retrieval-Augmented Generation with Large Language Models in Nephrology: Advancing Practical Applications", Medicina (Kaunas). 2024
[4] Zou et al., "PoisonedRAG: Knowledge Poisoning Attacks to Retrieval-Augmented Generation of Large Language Models", USENIX Security, 2025
---
Rebuttal Comment 1.1:
Comment: I appreciate the clarifications on the experimental setup, orthogonal augmentation, and retriever choices. However, I still have a few concerns:
1. Although attackers typically target a small set of queries, defenders do not know in advance which ones will be attacked. In practice, this means defenders must aim to protect as many queries as possible. Moreover, the assumption that defenders have access to clean, unpoisoned documents may be difficult to guarantee, especially in settings where poisoning is possible.
2. As mentioned earlier in Questions, many retrieval systems adopt Doc2Query, where queries are appended to clean documents. This could significantly impact both the paper’s conclusions and the effectiveness of the proposed defense.
Therefore, I am inclined to maintain my current score. | Summary: The paper explores the vulnerability of Retrieval-Augmented Generation (RAG) systems, specifically in knowledge-intensive domains like medical and legal Q&A. The authors demonstrate that retrieval models used in RAG are susceptible to universal poisoning attacks, where adversaries inject manipulated documents into a corpus to influence retrieval outcomes. By conducting extensive experiments across 225 different combinations of corpus, retriever, query, and targeted information, they reveal how poisoned documents can consistently be retrieved at high ranks. The paper further investigates the underlying reasons for this vulnerability, introducing the concept of orthogonal augmentation, which explains how document embeddings are manipulated to maintain high similarity with queries. To mitigate this risk, the authors propose a detection-based defense mechanism leveraging Mahalanobis distance and covariance shrinkage, demonstrating high success rates in identifying poisoned documents.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes
Relation To Broader Scientific Literature: The paper proposes a poisoning attack for RAG.
Essential References Not Discussed: Yes
Other Strengths And Weaknesses: Strength
- The paper highlights a crucial security issue in retrieval-based systems, especially in sensitive fields like healthcare and legal AI applications, where misinformation or adversarial manipulation can have serious consequences.
- The work presents an insightful observation about how dense retrieval models process concatenated adversarial text, offering a new perspective on why poisoning attacks succeed.
- The paper explores variations of the attack, including paraphrased queries, showing that the attack remains effective even when exact query matches are unavailable.
Weakness
- Lack of Novelty. The method appears to be simply an integration of a poisoning attack within RAG, where the attacker-defined query consistently results in a high-ranking retrieval of the poisoned document.
- Although the paper partly relaxes the assumption by showing robustness under paraphrasing, the attack still relies on knowing the typical structure of medical queries.
- The proposed detection method based on Mahalanobis distance with covariance shrinkage appears effective empirically; however, its performance may be highly sensitive to the choice of the shrinkage parameter (β) and the quality of the anchor set.
Other Comments Or Suggestions: See the Weakness
Questions For Authors: See the Weakness
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewers for investing their time and effort in reviewing our manuscript and providing valuable feedback. We will address their comments point by point in the following and incorporate them into our revision.
>Q: Lack of Novelty. The method appears to be simply an integration of a poisoning attack within RAG, where the attacker-defined query consistently results in a high-ranking retrieval of the poisoned document.
**R**: The novelty of our work lies in the following aspects:
- We systematically investigate and comprehend the robustness of retrieval systems employed in RAG, by introducing a new attack. We achieve this by injecting various types of information, encompassing both irrelevant and relevant content, into the corpus and evaluating the ease or difficulty of retrieval.
- We propose the `orthogonal augmentation` property to explain the wide-spread success of the attack, and provide empirical evidence to support this property.
- We propose a new defense based on the `orthogonal augmentation` property, which can effectively filter out the adversarial documents.
Given the relatively new development of safety in RAG, e.g., poisoning attacks, we do believe the above listed contributions are novel and valuable. We will clarify this in the revised version.
>Q: Although the paper partly relaxes the assumption by showing robustness under paraphrasing, the attack still relies on knowing the typical structure of medical queries.
**R**: We have included additional experiments on the *legal domain* in Table 10 in Section D of the supplementary material. Overall, we observe similar attack success rates in the legal domain as in the medical domain presented in the main text. Therefore, we believe that the proposed attacks can be generalized to a wide range of domain applications. We will clarify this in the revision.
>Q: The proposed detection method based on Mahalanobis distance with covariance shrinkage appears effective empirically; however, its performance may be highly sensitive to the choice of the shrinkage parameter (β) and the quality of the anchor set.
**R**: We have included an ablation study on the selection of $\beta$ in Table 8 in Section C of the supplementary material. We observed that the detection performance remains stable across a wide range of $\beta$ selections. Regarding the anchor set, if the anchor set is non-informative, it becomes theoretically infeasible to implement any effective defenses. We will include more discussions and empirical results in the main text.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for their detailed responses. The authors have addressed most of my concerns. Despite the (still) limited novelty, I raise my score. | Summary: This paper demonstrates the vulnerability of retrieving systems in RAG to universal poisoning attacks. Through examples in medical Q&A, the paper reveals that due to the orthogonal augmentation property, the deviation from the query’s embedding to that of the poisoned document tends to only shift in the orthogonal direction, which means that the poisoned document and the query retain high similarity, therefore enabling successful retrieval and poisoning attacks. Based on these findings, the paper develops a new detection-based defense, achieving a high level of accuracy.
Claims And Evidence: The paper makes key claims that due to the orthogonal augmentation property of the embeddings, the high similarity of the poisoned document and query can be maintained, enabling the poisoning attacks. The claim is backed by experiments on multiple dense retrievers (e.g., Contriever and MedCPT) using the MedQA dataset. By changing the lengths and similarities of 𝑝 relative to
𝑞 and measured four different similarity metrics, the results show that as inner product $𝑓(𝑞)^𝑇𝑓(𝑝)$ decreases, the concatenated embedding remains largely aligned with 𝑓(𝑞) (with an angle close to 90° for the augmentation vector 𝑣), and support the theoretical claim.
One weakness is that the orthogonal augmentation property relies on the behavior of the embedding function, specifically its approximate linearity under concatenation. Given that Contriever and MedCPT have different sensitivity to document length, the claim might vary with retrieval architecture or training regimes, and does not necessarily support the notion of "universal".
The other weakness is that another underlying assumption for the claim is that the concatenated adversarial information is nearly orthogonal to the original query, but that might not be the case and being orthogonal does not necessarily mean the underlying documents are semantically unrelated.
Methods And Evaluation Criteria: This paper proposes the vulnerability of the RAG systems to poisoning attacks, and measures the success rate of attacks with the appropriate ablation study of the K first top results. The methods and evaluation criteria make sense for the main claim. However, for the new detection mechanism, the paper only measures precision but not recall of the new detection mechanism.
Theoretical Claims: There is no theoretical claim in this paper.
Experimental Designs Or Analyses: The experimental designs are sound based on the best of my knowledge.
Supplementary Material: I have reviewed all supplementary materials - the authors mention that the details of the retrievers are in the appendix but I have not found those details.
Relation To Broader Scientific Literature: Essential references related to this paper include previous works on RAG systems and adversarial attacks on RAG. The authors are able to cite a few key works in the field and clarify their unique contributions specific to the adversarial attacks on retrieval part of RAG and specific knowledge domain in healthcare.
Essential References Not Discussed: There are other literature regarding LLM poisoning attacks.
Other Strengths And Weaknesses: This paper is clear, well-motivated and the research direction has tremendous impact to real-world AI applications.
Other Comments Or Suggestions: N/A
Questions For Authors: - The authors select three retrievers based on their their general ability / domain design. Does it make sense to have retrievers that have more architectural / training regime variations?
- The authors mention that they check the general attack areas / target datasets by using GPT-3 to check their semantic closeness. It could be helpful to include some summary in the appendix?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewers for investing their time and effort in reviewing our manuscript and providing valuable feedback. We will address their comments point by point in the following and incorporate them into our revision.
>Q: One weakness is that the orthogonal augmentation property relies on the behavior of the embedding function, specifically its approximate linearity under concatenation. Given that Contriever and MedCPT have different sensitivity to document length, the claim might vary with retrieval architecture or training regimes, and does not necessarily support the notion of "universal". The authors select three retrievers based on their general ability / domain design. Does it make sense to have retrievers that have more architectural / training regime variations?
**R**: The three retrievers used in our paper themselves have different architectures and training regimes. For example, the Contriever is a single-tower model with contrastive learning training regime, i.e., InfoNCE loss, trained on general purpose domain data. While the MedCPT is a cross-encoder re-ranker model with two-stage training (InfoNCE for contrastive learning + cross-entropy for reranker) for medical purposes. We will add results on closed-source models like text-embedding-3 from OpenAI (shown in Table below) in the revised version to further validate the generality of our findings.
Table. Top 2 retrieval success rates with text-embedding-3 as the retriever and MedMCQA, PubMedQA as the query corpus.
| Corpus | Attack Success Rate |
|--------------------|---------------------|
| Textbook | 0.95 |
| StatPearls | 0.90 |
| PubMed | 0.83 |
>Q: The other weakness is that another underlying assumption for the claim is that the concatenated adversarial information is nearly orthogonal to the original query, but that might not be the case and being orthogonal does not necessarily mean the underlying documents are semantically unrelated.
**R**: We thank you for your extremely sharp comments. We addressed this point in Lines 352 - 362 (left) of the main text. We found that closeness to orthogonality between embeddings **does not** imply that their associated documents are semantically irrelevant. For example, we randomly sampled two nonoverlapping batches of questions from the MedQA dataset and found that the angle between their embeddings is around $70^\circ$. Yet, these batches of queries are all semantically related to biology research questions. As a result, we believe the stated assumption is reasonable to a certain degree. We will further clarify this in the revised version.
>Q: The authors mention that they check the general attack areas / target datasets by using GPT-3 to check their semantic closeness. It could be helpful to include some summary in the appendix?
**R**: We will include the summary of the semantic closeness check in the appendix as you suggested.
>Q: I have reviewed all supplementary materials - the authors mention that the details of the retrievers are in the appendix but I have not found those details.
**R**: We will include the details of the retrievers in the appendix as you suggested. | null | null | null | null |
DANCE: Dual Unbiased Expansion with Group-acquired Alignment for Out-of-distribution Graph Fairness Learning | Accept (poster) | Summary: This paper propose DANCE to improve fairness performance of GNNs under distribution shifts. DANCE addresses two key challenges: sensitive group imbalance and the trade-off between fairness and model performance. DANCE uses unbiased mixup to balance sensitive attributes, fairness-aware adversarial learning to improve robustness, and a group-acquired alignment strategy to prioritize fair representations by considering sensitive attributes. Extensive experimental results show the effectiveness of DANCE.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes, all parts.
Relation To Broader Scientific Literature: Graph neural networks (GNNs), fairness in machine learning, and out-of-distribution (OOD) generalization.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. This paper addresses graph fairness under distribution shifts, a problem that remains largely unexplored.
2. DANCE expands the training distribution in both graph structure and feature space, generating challenging yet unbiased virtual data.
3. Extensive experiments demonstrate the effectiveness of DANCE
4. This paper provides a theoretical analysis of the graph diffusion process, showing how it controls information propagation across different sensitive groups.
Weaknesses:
1. High computational cost. DANCE use multiple modules (graph expansion, adversarial learning, alignment, and disentanglement), which increase computational costs.
2. The authors do not provide case studies that illustrate why DANCE is superior than other methods.
Other Comments Or Suggestions: 1. The authors should provide theoretical analysis or case studies to show why DANCE is superior than other methods.
2. The authors should provide complexity analysis.
Questions For Authors: Please refer to the suggestions
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We are truly grateful for the time you have taken to review our paper, your insightful comments and support. Your positive feedback is incredibly encouraging for us! In the following response, we would like to address your major concern and provide additional clarification.
> Q1. High computational cost. DANCE use multiple modules (graph expansion, adversarial learning, alignment, and disentanglement), which increase computational costs.
Thanks for your comment. We have included the efficiency analysis and comparison as follows. From the result, we can observe that our method has a competitive computation cost. In particular, we provide the following analysis:
- **Complexity analysis.** The computing complexity of our framework mainly depends on (a) **Dual graph expansion**, (b) **Group-acquired alignment** and (c) **Representation disentanglement**. Let $N_{syn}$ be the number of synthesized nodes. Then, since logits can be obtained from the previous epoch, for (a), we need $\mathcal{O}(N^2_{syn})$ extra time for anchor and auxiliary nodes sampling, $\mathcal{O}(N_{syn}d)$ for feature mixup and $\mathcal{O}(N_{syn}/N\cdot|\mathcal{E}|)$ for generating synthesized edges. Meanwhile, adversarial learning on synthesized data takes $\mathcal{O}((N+N_{syn})d^2)$. For (b) and (c), the complexity for the target and sensitive encoder is $\mathcal{O}(2L|\mathcal{E}|d+2Nd^2)$ with $L$ layers while the view alignment takes $\mathcal{O}(N|\mathcal{B}|d)$ with total $|\mathcal{B}|$ positive and negative pairs. Compared with FatraGNN [1], the additional complexity is $\mathcal{O}({N}^2_{syn}+(N_{syn}+N|\mathcal{B}|)d+N_{syn}/N\cdot|\mathcal{E}|)$, mainly from the dual graph augmentation and contrastive learning modules, which are carefully controlled in our implementation.
- **Practical training overhead.** From a practical standpoint, we have provided the time complexity and training time of our DANCE to further demonstrate its computational efficiency in comparison to other baselines. The results indicate that our framework maintains a competitive computation cost compared with baselines.
|Model| Params (M) |Training Time (s/epoch on Credit)|
|-|-|-|
|FatraGNN |0.140| 0.263 |
|DANCE |0.536| 0.340 |
In summary, our method has a **competitive computation cost** in comparison with the baseline. We will include the above discussion in our revised version.
> Q2. The authors do not provide case studies that illustrate why DANCE is superior than other methods.
Thank you for the insightful comment! We have provided **t-SNE visualizations that offer a qualitative comparison of the learned representations** between DANCE and the benchmark model (FatraGNN). These visualizations help illustrate how DANCE better achieves fair and discriminative representations.
The colors in the plots represent different combinations of sensitive attributes and target labels:
- **Pink**: sensitive = 1, y = 0
- **Green**: sensitive = 0, y = 0
- **Grey**: sensitive = 1, y = 1
- **Blue**: sensitive = 0, y = 1
**FatraGNN [1] (Benchmark) t-SNE Results**:
Pokec_z: https://anonymous.4open.science/r/DANCE_ICML_2025-BD70/Fatra_pokec_z_tsne.png
Pokec_n: https://anonymous.4open.science/r/DANCE_ICML_2025-BD70/Fatra_pokec_n_tsne.png
**DANCE t-SNE Results**:
Pokec_z: https://anonymous.4open.science/r/DANCE_ICML_2025-BD70/DANCE_pokec_z_tsne.png
Pokec_n: https://anonymous.4open.science/r/DANCE_ICML_2025-BD70/DANCE_pokec_n_tsne.png
Compared to FatraGNN, **DANCE exhibits a much clearer separation between target labels** (i.e., the blue/grey cluster vs. the pink/green cluster), **while sensitive attributes are not clustered, indicating reduced sensitive information leakage**. In contrast, the benchmark method (FatraGNN) shows all four colors more uniformly mixed, with no clear separation based on target labels, suggesting entanglement of sensitive and target information.
This case study provides intuitive evidence that DANCE achieves better separation of semantic information while mitigating bias from sensitive attributes, thereby demonstrating its superiority over existing methods.
**Reference**
[1] Li Y, Wang X, Xing Y, et al. Graph fairness learning under distribution shifts, Proceedings of the ACM Web Conference 2024. 2024: 676-684.
Thanks again for appreciating our work and for your constructive suggestions. Please let us know if you have further questions.
---
Rebuttal Comment 1.1:
Comment: Thanks for your explanation. Most of the concerns have been solved. I will raise the score. | Summary: This paper proposes DANCE, a novel framework for enhancing graph neural network fairness learning under distribution shifts by generating unbiased virtual graph data through dual expansion (structural and feature-based) and aligning node representations. It specifically tackles sensitive group imbalance and fairness-performance conflicts by synthesizing challenging yet unbiased virtual graphs and disentangling sensitive attributes. Experiments demonstrate the method's superiority in fairness and generalization performance over existing fairness-aware GNNs.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: They appear to be generally correct and the intuition makes sense to me as well.
Experimental Designs Or Analyses: They appear to be carefully designed and I do not have major complaints about the experimental designs and analyses.
Supplementary Material: Yes, mostly A and B
Relation To Broader Scientific Literature: This paper is properly positioned as a part of the broader scientific literature with clarifications about the relationship between itself and other works.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
1 - This paper Introduces dual unbiased expansion strategies in both graph and hidden spaces to address distribution shifts.
2 - The idea of group-acquired alignment explicitly focusing on fairness is interesting, particularly handling minority-sensitive groups.
3 - Comprehensive framework including both adversarial modules and representation disentanglement strategies.
4 - Strong empirical validation across multiple benchmark datasets showcasing clear improvements over baselines.
5 - Addresses a realistic and underexplored challenge in graph fairness research by focusing on distribution shifts.
Weaknesses:
1 - The framework involves multiple sophisticated modules, potentially increasing the difficulty of implementation and complexity. Also, the author did not discuss the time complexity for the proposed method: how expensive it is to adopt it in practice? Generally the discussions on computational cost, scalability, and efficiency is limited.
Other Comments Or Suggestions: N/A
Questions For Authors: What are the computational overheads introduced by the proposed approach, particularly in comparison to simpler fairness-aware methods?
I would be interested in the details about the rationale behind prioritizing negative pairs with identical sensitive labels in the group-acquired alignment objective. Plus, how significantly does this choice affect fairness outcomes?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We are truly grateful for the time you have taken to review our paper, your insightful comments and support. Your positive feedback is incredibly encouraging for us! In the following response, we would like to address your major concern and provide additional clarification.
>Q1. The framework involves multiple sophisticated modules, potentially increasing the difficulty of implementation and complexity. Also, the author did not discuss the time complexity for the proposed method: how expensive it is to adopt it in practice? Generally the discussions on computational cost, scalability, and efficiency is limited. What are the computational overheads introduced by the proposed approach, particularly in comparison to simpler fairness-aware methods?
Thanks for your comment. We have included the efficiency analysis and comparison as follows. From the result, we can observe that our method has a competitive computation cost. In particular, we provide the following analysis:
- **Complexity analysis.** The computing complexity of our framework mainly depends on (a) **Dual graph expansion**, (b) **Group-acquired alignment** and (c) **Representation disentanglement**. Let $N_{syn}$ be the number of synthesized nodes. Then, since logits can be obtained from the previous epoch, for (a), we need $\mathcal{O}(N^2_{syn})$ extra time for anchor and auxiliary nodes sampling, $\mathcal{O}(N_{syn}d)$ for feature mixup and $\mathcal{O}(N_{syn}/N\cdot|\mathcal{E}|)$ for generating synthesized edges. Meanwhile, adversarial learning on synthesized data takes $\mathcal{O}((N+N_{syn})d^2)$. For (b) and (c), the complexity for the target and sensitive encoder is $\mathcal{O}(2L|\mathcal{E}|d+2Nd^2)$ with $L$ layers while the view alignment takes $\mathcal{O}(N|\mathcal{B}|d)$ with total $|\mathcal{B}|$ positive and negative pairs. Compared with FatraGNN [1], the additional complexity is $\mathcal{O}({N}^2_{syn}+(N_{syn}+N|\mathcal{B}|)d+N_{syn}/N\cdot|\mathcal{E}|)$, mainly from the dual graph augmentation and contrastive learning modules, which are carefully controlled in our implementation.
- **Practical training overhead.** From a practical standpoint, we have provided the time complexity and training time of our DANCE to further demonstrate its computational efficiency in comparison to other baselines. The results indicate that our framework maintains a competitive computation cost compared with baselines.
|Model| Params (M) |Training Time (s/epoch on Credit)|
|-|-|-|
|FatraGNN |0.140| 0.263 |
|DANCE |0.536| 0.340 |
In summary, our method has a **competitive computation cost** in comparison with the baseline. We will include the above discussion in our revised version.
>Q2. The rationale behind prioritizing negative pairs with identical sensitive labels.
Thanks for your comment. Below we provide both the rationale analysis and empirical evidence to support prioritizing negative pairs with identical sensitive attributes in the group-acquired alignment objective.
- **Rationale Analysis.** The rationale behind prioritizing the negative pairs is to mitigate the encoder’s reliance on sensitive attribute information during representation learning. When $ z _ p\in\mathbf{Z} _ {ig} $, both **the positive and negative samples share the same sensitive attributes as the anchor node**. Therefore, the encoder no longer considers sensitive attribute information a valuable feature for fairness learning. When $ z _ p\in\mathbf{Z} _ {sg} $, the **positive samples have different sensitive attributes from both the anchor and the negative samples**. If the encoder learns sensitive attribute information, the similarity between the positive samples and the anchor will decrease, while the similarity between the negative samples and the anchor will increase, which is contrary to the objective of the loss function.
- **Empirical Evidence.** To validate this design, we performed a comparative experiment where **negative pairs were sampled solely based on differing target labels, without considering sensitive attributes** (denoted Var 1 in the following table). The results are summarized below:
| Dataset | Metric |Var1|DANCE|| Dataset | Metric| Var1 | DANCE|
|-|-|-|-|-|-|-|-|-|
|**Pokec_z**| ACC↑|71.8|70.09||**Pokec_n**| ACC↑|67.49|66.58|
|| ROC-AUC↑|78.16|77.42|||ROC-AUC↑|74.32|72.88|
||△DP ↓| 5.71|3.74|||△DP ↓|1.77|0.83|
||△EO ↓| 3.33 |2.70|||△EO ↓|1.57|0.29|
From the result, we can find DANCE significantly outperforms Var 1 on fairness metrics. This indicates that **prioritizing negative pairs with identical sensitive attributes** plays a key role in learning representations that are both fair and robust under distribution shifts.
**Reference**
[1] Li Y, Wang X, Xing Y, et al. Graph fairness learning under distribution shifts, Proceedings of the ACM Web Conference 2024. 2024: 676-684.
Thanks again for appreciating our work and for your constructive suggestions. Please let us know if you have further questions. | Summary: The paper proposes a method to improve fairness in graph neural networks (GNNs) under distribution shifts. It introduces dual graph expansion to generate unbiased virtual graph data, group-acquired alignment to prioritize negative pairs with identical sensitive labels, and representation disentanglement to separate sensitive attributes from task-related information. Experiments show that DANCE improves both fairness and classification performance compared to existing methods.
Claims And Evidence: Yes. The claims are reasonable and convincing.
Methods And Evaluation Criteria: Yes, the methods and evaluation make sense.
Theoretical Claims: Yes. The proofs seems correct.
Experimental Designs Or Analyses: I have some concerns about the experiments.
1. Although the paper focus on the distribution shift situation, it is worthwhile to see the performance under the same distribution.
2. The ablation study is very confusing. For example, all Var1 to Var4 (in table 3) have significant degrade with respect to the fairness metrics. Does it means every component, even the mixup, will contribute to the fairness results? I doubt it.
3. There are some contradict results, for example, in table 3, while C3-Var3 cell has better $\Delta DP$ performance, other cells (C-Var3) show significant lower performance. The authors did not explain that in the paper.
Supplementary Material: Yes.
Relation To Broader Scientific Literature: The key contributions of the DANCE framework build upon and extend several lines of research in fair graph learning, out-of-distribution (OOD) generalization, and adversarial learning for fairness. FatraGNN also deals with a similar problem, but this work achieves better performance.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: Strengths:
1. The topic and problem is realistic and interesting.
2. The experiments are extensive.
Weakness:
1. Please refer to the concerns in Experiment above.
2. The methods have limited novelty. The Graph Expansion and Attributes Disentanglement are studied in existing IID fair graph learning, although transferring it to OOD graph learning is novel.
Other Comments Or Suggestions: Please use the same precision in the table.
Questions For Authors: Please refer to the weakness.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are truly grateful for the time you have taken to review our paper, your insightful comments and support. Your positive feedback is incredibly encouraging for us! In the following response, we would like to address your major concern and provide additional clarification.
> Q1. The performance under the same distribution.
Thank you for your comment. We have added the performance of our model and several baselines under the same distribution setting as below. From the results, our method achieves better performance compared with baselines. We will add these results to our revised version.
|Dataset|Metric|FatraGNN|DANCE|Dataset|Metric|FatraGNN|DANCE|
|-|-|-|-|-|-|-|-|
|**c1**| ACC↑|78.11| 80.43|**c2**| ACC↑| 77.81|80.05|
||ROC-AUC↑| 65.59| 74.69 || ROC-AUC↑|68.92|81.23|
||△DP ↓| 6.88| 4.49 ||△DP ↓| 1.04|1.83|
||△EO ↓| 4.56| 3.76 ||△EO ↓|1.64|1.91|
| **c3** | ACC↑|72.39|80.77|**c4**| ACC↑| 72.98| 76.38 |
||ROC-AUC↑ | 71.24| 83.21 || ROC-AUC↑ | 71.76| 76.80 |
||△DP ↓|1.80| 2.64||△DP ↓| 3.09| 3.47|
||△EO ↓|1.48| 6.00||△EO ↓|2.07| 2.60|
> Q2. Does it mean every component, even the mixup, will contribute to the fairness results?
Thank you for the comment. In our framework, each component is designed to address a specific challenge in out-of-distribution (OOD) graph fairness learning, and our ablation results demonstrate that each module makes a meaningful contribution to the final fairness performance.
Specifically, we expand the graph data in **both the structural space and the feature space**. The **unbiased Mixup** module enlarges the decision boundary of minority groups, helping to rebalance representation across sensitive attributes. The **adversarial learning** module simulates worst-case distribution shifts by introducing challenging perturbations in feature space, enhancing the model's robustness. Building on this expanded data, the **group-acquired alignment** module aligns representations across groups while discouraging the use of sensitive attributes, and the **representation disentanglement** module explicitly separates sensitive and target information to further reduce bias.
Together, these components form a cohesive design, and the degradation observed in fairness metrics upon removing any one of them confirms that each module plays a critical role in achieving fairness under distribution shifts.
> Q3. In Table 3, while the C3-Var3 cell has better $ \Delta DP $ performance, other cells (C-Var3) show significantly lower performance
Thank you for the comment. We have provided the following explanation:
- **Complicated Graph Data**. Real-world graph datasets (such as Credit-Cs) exhibit considerable variability in their structural properties—such as homophily and sensitive group imbalance.
As shown in the table below, these graph datasets have different and complicated characteristics, which could result in performance fluctuation. Overall, our full model shows better performance in comparison with the model variant in most cases, which validates the effectiveness of the proposed method.
|Dataset|Sensitive Homophily|s0 Internal Edge Ratio|s1 Internal Edge Ratio|Cross-group Edge Ratio|
|-|-|-|-|-|
|C1|0.821| 0.777|0.044|0.179|
|C2|0.807| 0.774|0.033|0.193|
|C3|0.755| 0.702|0.053|0.245|
|C4|0.737| 0.681|0.057|0.262|
- **Previous Observations**. Similar cross-dataset variations have been observed in prior studies. For instance, [2] observes that fairness improvements can vary significantly across different datasets when evaluating fairness-aware GNN methods.
As shown in Table 1 of [2], RFR exhibits large fluctuations in $\Delta$DP between the Adult (1.0, 2.0) and Adult (3.0, 6.0) subsets, while its $\Delta$DP performance remains relatively stable across the ACS-E (1.0, 2.0) and ACS-E (3.0, 6.0) subsets. This illustrates that the underlying data distribution plays a crucial role, and that fairness improvements achieved on one subset may not generalize consistently across others.
> Q4. Novelty of DANCE
Thanks for your comment. The innovations of this work include:
- **Data-centric perspective**. We explore an underexplored yet important OOD graph fairness learning problem from a data-centric perspective, achieving better performance compared to baselines.
- **A unified graph fairness learning framework**. Our framework is a unified approach that combines dual unbiased graph expansion and group-acquired alignment to minimize the domain gap while ensuring fairness.
- **Theoretical analysis**. We provide a theoretical analysis demonstrating that our framework can control information propagation between different groups for fairness learning and ensure the convergence of the loss function.
[1] Laclau C, et al. A survey on fairness for machine learning on graphs. arXiv, 2022.
[2] Jiang et al., Chasing fairness under distribution shift: A model weight perturbation approach, NeurIPS 2023.
Thanks again for appreciating our work and for your constructive suggestions. | Summary: This paper proposes the DANCE method, which aims to address the problem of fair learning of graph neural networks (GNNs) under distributional bias. Traditional methods assume that training and testing data are identically distributed, whereas distribution bias is prevalent in real-world scenarios, leading to degradation of model fairness and performance.The core idea of DANCE is to generate unbiased and challenging virtual graph data in structural and feature space to simulate distributional bias and enhance model robustness through a data-centric perspective.
Claims And Evidence: Experiments on real-world datasets demonstrate that DANCE outperforms baseline methods in both classification performance and fairness metrics .
Methods And Evaluation Criteria: The OOD issue is really a common problem in reality.
Theoretical Claims: I am not really sure why Theorem 3.1 can show that the graph diffusion method can precisely control the propagation of information between different groups, could the authors explain this in further detail?
Experimental Designs Or Analyses: The experimental design is sound.
Supplementary Material: The appendix is supplemented with some experimental results and definitional proofs.
Relation To Broader Scientific Literature: This has implications for the de-biasing of graph representation learning.
Essential References Not Discussed: Some of the work on fair graph learning [1,2,3] also involves data reconstruction, which the authors should include.
[1]"Rethinking fair graph neural networks from re-balancing." Proceedings of the 30th ACM SIGKDD Conference on Knowledge Discovery and Data Mining. 2024.
[2] "Disentangled contrastive learning for fair graph representations." Neural Networks 181 (2025): 106781.
[3]"Toward fair graph neural networks via real counterfactual samples." Knowledge and Information Systems 66.11 (2024): 6617-6641.
Other Strengths And Weaknesses: Strengths:
This paper provides a principled basis for linking graph diffusion theory to fairness, which is an inspiration for the fair graph learning community.
Weaknesses:
The author claims ‘The core idea of our DANCE is to generate challenging yet unbiased virtual graph data in both graph
and hidden spaces...’ but does not define ‘challenging’. What is to be understood by ‘challenging’ in this context?
Other Comments Or Suggestions: None
Questions For Authors: Please refer to previous comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We are truly grateful for the time you have taken to review our paper and your insightful review. Here we address your comments in the following.
>Q1. Why Theorem 3.1 can show that the graph diffusion method can precisely control the propagation of information between different groups?
To clarify the intuition behind the assumption in Theorem 3.1, we rewrite it as follows:
First, we prove that for any $i \in \mathcal{V} _ s$, there exists $j \in \mathcal{V} _ {-s}$ such that:
$$
\left[\sum _ {r=0}^{\infty} \theta^r ({T} _ {\text{anc}}^r {H}^{(l-1)})\right] _ {ij} \neq 0.
$$
By the definition of $A _ {anc}$, for any $i \in \mathcal{V} _ s$ we can get $A _ {anc,ik} > 0$, where $k \in \mathcal{V} _ s \cup \{v _ {syn}\}$. And there exists $j \in \mathcal{V} _ {-s}$ satisfying $A _ {anc,v _ {syn}j} > 0$. This implies that for any $i \in \mathcal{V} _ s$, there exists a path $i \to v _ {syn} \to j$ with $j \in\mathcal{V} _ {-s}$, where $A _ {anc,iv _ {syn}} > 0$ and $A _ {anc,v _ {syn}j} > 0$. For path length $r _ 0 = 2$, we can get $[T _ {anc}^2] _ {ij} = \sum _ {k \in V} [T _ {anc}] _ {ik}[T _ {anc}] _ {kj} \\
\geq \frac{A _ {anc,iv _ {syn}}}{D _ {anc,i}} \cdot \frac{A _ {anc,v _ {syn}j}}{D _ {anc,v _ {syn}}} > 0$. Similarly, for $r _ 0 > 2$ with the path $i = k _ 0 \to k _ 1 \to \cdots \to k _ {r _ 0} = j$, we have $[T _ {anc}^{r _ 0}] _ {ij} \geq \prod _ {s=1}^{r _ 0} \frac{A _ {anc,k _ {s-1}k _ s}}{D _ {anc,k _ {s-1}}} > 0$. Therefore, we can get $\left[\sum _ {r=0}^\infty \theta _ r (T _ {anc}^r H^{(l-1)})\right] _ {ij} > 0$.
Then, we prove by mathematical induction that $\forall i \in \mathcal{V} _ {-s}, j \in \mathcal{V} _ s$, we have:
$$
\left[\sum_{r=0}^\infty \theta_r (T_{anc}^r H^{(l-1)})\right]_{ij} = 0.
$$
**Base case ($r=0$)**: For $i \in \mathcal{V} _ {-s}$ and $j \in \mathcal{V} _ s$, the identity matrix satisfies $[T _ {anc}^0] _ {ij} = \delta _ {ij} = 0.$
**Inductive step**: Assume $\forall r \leq n$ and $\forall i \in \mathcal{V} _ {-s}$, $j \in \mathcal{V} _ {s}$, $[T _ {anc}^r] _ {ij} = 0$. For $r = n+1$, we have $[T _ {anc}^{n+1}] _ {ij} = \sum _ {k \in \mathcal{V} _ s} [T _ {anc}^n] _ {ik}[T _ {anc}] _ {kj} + \sum _ {k \in \mathcal{V} _ {-s}} [T _ {anc}^n] _ {ik}[T _ {anc}] _ {kj}$.
$ \forall k \in \mathcal{V} _ {s} $, the inductive hypothesis implies $ [T _ {anc}^n] _ {ik} = 0 $. $ \forall k \in \mathcal{V} _ {-s}$, by the definition of $A _ {anc}$, $A _ {anc,kj}=0$. Therefore, we can get $[T _ {anc}^{n+1}] _ {ij} = 0$.
By mathematical induction, $ \forall r \geq 0 $, $[T _ {anc}^r] _ {ij} = 0$, which leads to $\left[\sum _ {r=0}^\infty \theta _ r (T _ {anc}^r H^{(l-1)})\right] _ {ij} = 0$.
This assumption reflects that **the graph diffusion method in DANCE can shield minority groups from majority interference while permitting essential cross-group feature learning**. This distinction justifies the assumption and highlights the geometric intuition behind Theorem 3.1.
>Q2. Some essential references are not included.
We will include the following discussion into our revised version:
```
Additionally, FairGB [1] introduces a counterfactual node mixup strategy, generating synthetic samples by interpolating node features and labels across different demographic groups to address demographic group imbalances. Similarly, FDGNN [2] and RFCGNN+ [3] design counterfactual augmentations by varying sensitive or label values while preserving the original adjacency matrices to learn fairer representations. In comparison with these methods, our method specifically focuses on mixing minor sensitive group nodes with those of different sensitive attributes to generate challenging samples that extend decision boundaries, thereby enhancing generalization and fairness.
```
>Q3. What is to be understood by ‘challenging’ in this context?
In our context, we use the term “challenging” samples to refer to those that are difficult to classify but strategically designed to improve generalization and fairness. Specifically:
- **Synthesized nodes located near class decision boundaries are generated via Mixup** (Eq. 7) between minor group nodes and auxiliary nodes. These samples **exhibit higher prediction uncertainty and encourage the model to refine its classification boundaries [4]**.
- **Adversarial learning (Sec. 3.2) introduces perturbations that further amplify this uncertainty**, thereby enhancing the model’s robustness and fairness under distribution shifts.
In summary, “challenging” refers to samples that are difficult to classify but strategically beneficial for improving both generalization and fairness.
[1] Rethinking fair graph neural networks from re-balancing. KDD 2024
[2] Disentangled contrastive learning for fair graph representations. Neural Networks, 2025
[3] Toward fair graph neural networks via real counterfactual samples. KAIS, 2024
[4] Self-supervised graph-level representation learning with adversarial contrastive learning, TKDD, 2023 | null | null | null | null | null | null |
Breaking the Barrier of Hard Samples: A Data-Centric Approach to Synthetic Data for Medical Tasks | Accept (poster) | Summary: This paper introduces a novel approach to synthetic data generation, leveraging a combination of statistical modeling and generative techniques to produce high-fidelity, diverse datasets for machine learning applications. The proposed methodology is designed to enhance the realism and utility of synthetic data, thereby improving model performance in data-scarce or privacy-sensitive scenarios. Through extensive experimentation, the authors demonstrate the proposed framework’s advantages over existing data synthesis techniques.
## update after rebuttal
Given these clarifications, most of my concerns have largely been resolved. As my initial score leaned towards acceptance, I decided to maintain it.
Claims And Evidence: The claims are generally supported by experimental results, though certain aspects warrant further substantiation:
- While the paper asserts that the generated synthetic data maintains both realism and diversity, it does not employ quantitative metrics such as Frechet Inception Distance (FID) or Maximum Mean Discrepancy (MMD) to evaluate these attributes rigorously.
- The choice of baseline models is not sufficiently justified. A more detailed discussion of the selection criteria for these baselines would strengthen the argument.
Methods And Evaluation Criteria: The paper employs standard evaluation methodologies for assessing synthetic data quality, yet some enhancements could improve the robustness of its findings:
- A more extensive analysis of the effect of synthetic data on downstream machine learning models (e.g., classification, regression) would provide deeper insight into its practical applicability.
Theoretical Claims: The paper does not introduce formal mathematical proofs, but the methodological framework appears sound. However, a theoretical discussion of the potential limitations—such as mode collapse in generative models or bias amplification in synthetic data—would strengthen the paper’s contribution.
Experimental Designs Or Analyses: Yes, the experimental setup is reasonable, but has certain limitations:
- The evaluation methodology relies heavily on qualitative visual assessments, which, while informative, should be supplemented with rigorous quantitative comparisons.
- The paper does not provide a thorough hyperparameter sensitivity analysis, making it difficult to assess the reproducibility and robustness of the proposed method.
Supplementary Material: Yes, the supplementary material was reviewed, with a focus on dataset descriptions and additional results. However, an ablation study is lacking to assess the contributions of individual components within the model.
Relation To Broader Scientific Literature: The work advances the field of data synthesis by proposing a new generative framework that balances realism and diversity. However, additional context is necessary to situate it within the broader literature:
- Recent **GAN-based and diffusion-based models** have addressed similar challenges in synthetic data generation, and a comparative discussion with these approaches would be beneficial.
- The paper does not thoroughly address techniques used for **synthetic data validation and bias mitigation**, which are critical in practical applications.
Essential References Not Discussed: Yes, the paper would benefit from discussing:
- State-of-the-art diffusion models and variational autoencoders (VAEs), which have demonstrated strong performance in synthetic data generation.
- Data augmentation and privacy-preserving synthetic data generation strategies, which are highly relevant to this research domain.
Other Strengths And Weaknesses: - Strengths: The proposed approach is well-motivated, tackling an important challenge in machine learning by improving the quality of synthetic datasets.
- Weaknesses: The lack of rigorous quantitative evaluation metrics and ablation studies limits the empirical contribution of the paper.
Other Comments Or Suggestions: - Some mathematical derivations would benefit from improved clarity and notation.
Questions For Authors: 1. How does the fidelity of the synthesized data compare to real-world distributions under rigorous statistical evaluation?
2. Would incorporating adversarial training or diffusion models further improve the quality and robustness of the generated data?
3. Can the authors elaborate on the scalability of their approach, particularly in the context of large-scale datasets?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: * **Ablation Studies and Components- Reviewers BQrC, VmCi**
We did not conduct an ablation study because the preprocessing step we adopted already serves as a form of comparison itself. Specifically, we chose to use our proposed preprocessing method as a comparison to traditional preprocessing techniques, such as feature selection and data cleaning, which are commonly used in the field. In our methodology, we intentionally selected a preprocessing approach that includes a profiling framework, which is optimized for each dataset. This framework is selected through an optimization process to identify the best preprocessing method for each dataset. We did not compare it to traditional preprocessing techniques like simple feature selection because those methods do not effectively capture the complexity and improvements our approach brings. Using our profiling framework as a baseline, we demonstrated the added value of combining it with a post-processing phase, significantly enhancing performance. Therefore, the methodology itself, through the comparison between our full approach (preprocessing + post-processing) and the chosen preprocessing method, already performs the role of an ablation study. We could have used a traditional feature selection method as the preprocessing step for comparison. Still, we are confident that our complete methodology provides the most effective solution. We believe the direct comparison between our full approach and a traditional preprocessing method already validates the effectiveness of our proposed methodology.
* **Fidelity Evaluation -- Reviewer VmCi**
We understand the concern regarding the reliance on qualitative visual assessments and the fidelity of the synthesized data compared to the real world. However, we emphasize that our evaluation includes rigorous quantitative analyses in addition to visual representations, which we believe enhance result interpretation.
Regarding evaluation metrics, we utilize the Root Mean Squared Error (RMSE) to assess the performance of predictive models and the Wasserstein distance to measure the similarity between real and synthetic data distributions. RMSE is a widely used metric for evaluating the accuracy of regression models, while the Wasserstein distance quantifies the representativeness of synthetic data. Additionally, we evaluate the quality of synthetic data based on three key criteria: Fidelity (accuracy), Diversity, and Generalizability.
Furthermore, we follow a rigorous evaluation protocol that includes Train on Synthetic, Test on Real (TSTR), and data augmentation strategies. We also employ the Kruskal-Wallis and Wilcoxon tests to assess the statistical validity of our results, ensuring the robustness of our evaluation.
Regarding the fidelity of the synthesized data compared to the real world, we used the Wasserstein distance, a robust statistical metric that computes the difference between distributions. This metric provides a meaningful and rigorous evaluation of the fidelity of synthetic data, enabling us to compare how well the synthesized data approximates real-world distributions.
Furthermore, the evolution of statistical values, such as mean, standard deviation, and quantiles, further supports the validity of our findings. We believe you may be referring to tests like the Kolmogorov-Smirnov (KS) test to assess the fidelity of distributions. However, we chose to adopt a single metric—the Wasserstein distance—due to its statistical rigor and ability to handle many experiments and other aspects analyzed in our work.
Additionally, the TSTR metric is not solely designed to evaluate whether synthetic data is useful for training models. Instead, it assesses whether the synthetic data distribution significantly differs from the original one. A large discrepancy between distributions would suggest that the model trained on synthetic data might perform poorly when tested on real data. Thus, the use of these metrics provides valuable insights without the need to collect an overwhelming number of additional metrics.
Wasserstein distance is widely used in the literature for such evaluations, and we believe it is sufficient for this purpose. Furthermore, when evaluating synthetic data, it is essential to consider not only fidelity but also diversity and generalization. By combining various evaluation protocols, we can comprehensively assess the usability of the synthetic data.
**Please review the response provided to reviewers sXia and fkDs, where we address your concern.**
Dear Reviewers VmCi, sXia, fkDs, and BQrC. We understand you are not required to look beyond the comments, but we addressed all points. Due to space limits, we prioritized common responses. A full reply, including additional comments, is in this PDF: https://anonymous.4open.science/r/icml2025-F9C4/Answers.pdf. We’d be grateful if you could check it.
---
Rebuttal Comment 1.1:
Comment: Thanks for your detailed rebuttal addressing my concerns.
The explanation regarding the ablation study—clarifying that the proposed framework in the preprocessing step effectively serves as a baseline for comparison—has provided a clearer understanding of the introduced methodology.
Additionally, your comprehensive justification for using RMSE, the Wasserstein distance, and TSTR, along with statistical tests to evaluate the fidelity of the synthesized data, does make sense.
**Given these clarifications, most of my concerns have largely been resolved. As my initial score leaned towards acceptance, I decided to maintain it.**
After checking the anonymous link you shared, I have two friendly suggestions:
1. Since external links have no length limits, consider creating a separate document for each reviewer. This makes it easier for them to find their responses.
2. The current PDF is a bit hard to read, the resolution is too low—Markdown might be clearer. | Summary: The paper focuses on generating training data for regression models in the medical domain. The proposed approach is based on two existing methods, which the authors refer to as Traditional Generative Techniques and PreProcess methods. In the Traditional approach, the method does not consider the difficulty distribution of the data during training, while the PreProcess method first categorizes the training data by difficulty and then trains separate generative models on each difficulty group. The final data set is created by merging the generated data from all models. The approach proposed in this paper combines both methods, training the generative model while considering data categorization and further filtering difficult samples after data synthesis to obtain the final dataset. Experiments on six datasets show that the proposed method effectively improves the quality of the synthetic dataset and reduces prediction errors in regression models.
### update after rebuttal:
I have read the authors' rebuttal as well as the reviews from the other reviewers. I appreciate the additional details provided. However, my main concerns were not fully resolved. As such, I will keep my original score, which already reflects a positive assessment.
Claims And Evidence: The primary claim of this paper, that the proposed framework can effectively synthesize training data for regression tasks in the medical domain and improve model prediction accuracy and generalization ability, is supported by evidence. The experimental results on six datasets, using various models, demonstrate the validity of the claim.
Methods And Evaluation Criteria: I believe the proposed methods and evaluation criteria are reasonable for the problem. The authors performed large-scale testing of their method on multiple benchmarks from the medical domain, using common metrics. They also evaluated the synthetic data’s ability to substitute real data and the quality of the generated data, exploring several relevant aspects.
Theoretical Claims: The paper does not present any theoretical claims or proofs.
Experimental Designs Or Analyses: The experimental designs and analyses presented in the paper seem sound. The authors validated their proposed method on sufficient datasets and models, analyzing three key aspects: whether the synthetic datasets can replace real data, whether they can be combined with real datasets, and the quality of the generated datasets themselves.
Supplementary Material: I reviewed the appendix section.
Relation To Broader Scientific Literature: The key contribution of this paper lies in its domain-specific focus on the medical field, emphasizing data-centric approaches in contrast to existing large language model-based generative pipelines that focus on general domain data generation. This focus addresses a gap in the current research direction.
Essential References Not Discussed: I believe the authors should have discussed recent methods for synthetic data generation using large language models (LLMs) and compared them to their proposed method. Below are some relevant surveys/papers:
Smolyak, D., et al. (2024). Large language models and synthetic health data: progress and prospects (JAMIA open 2024)
Li, R., et al. (2023). Two directions for clinical data generation with large language models: data-to-label and label-to-data. (EMNLP 2023)
Kumichev, G., et al. (2024). MedSyn: LLM-based Synthetic Medical Text Generation Framework. arXiv preprint arXiv:2408.02056
Seedat, N., et al. (2024). Curated LLM: Synergy of LLMs and Data Curation for tabular augmentation in low-data regimes (PMLR 2024)
Zhou, H., et al. (2024). A Survey of Large Language Models in Medicine: Progress, Application, and Challenge. arXiv:2311.05112
Other Strengths And Weaknesses: A major weakness of the paper is the innovation in its method. As mentioned in the paper, the proposed method is largely based on existing traditional and preprocess approaches. The primary innovation lies in the filtering of the generated data after synthesis, which may limit the contribution's significance.
Another weakness is the lack of comparison with recent methods for data generation or filtering using LLMs.
Other Comments Or Suggestions: I believe the writing of the paper could be improved, particularly in Sections 3 and 4 where the logical flow and method descriptions could be clearer. For example, the authors should first introduce the traditional and preprocess methods, then explain their differences, and finally describe their proposed workflow to enhance the readability of the paper.
Questions For Authors: Why not consider using any LLM-based methods during the data generation process?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: * **Hyperparameter Sensitivity- Revwers sXia, BQrC (Q1), VmCi**
The choice of the hard sample threshold is based on the performance of the profiling framework. In Appendix F, we provide a detailed explanation of this selection process. Specifically, the threshold is determined by identifying the best-performing framework in terms of F1-score across different levels of label flipping.
Once the best framework is identified, we use the corresponding threshold that yielded the highest F1-score to profile the data. This process occurs at both the pre-processing and post-processing stages. Since we always use the best-performing framework, we consider threshold selection a non-critical hyperparameter, as it is inherently optimized within the profiling stage.
Formally, let $ \mathcal{F} $ be the set of evaluated frameworks and $ \mathcal{T} $ the set of tested thresholds. The goal of the process described in the paper is to find the optimal pair $ (f^*, t^*) $ such that:
\begin{equation}
(f^*, t^*) = \arg\max_{f \in \mathcal{F}, t \in \mathcal{T}} \mathbb{E}[F1(f, t)]
\end{equation}
where $ \mathbb{E}[F1(f, t)] $ represents the average F1-score across different proportions of label flipping.
Sensitivity analysis typically involves testing the robustness of a fixed parameter, but in our case, $ t^* $ is not arbitrary — it is chosen as part of an optimization process that depends on $ f^* $. Since we have already found the optimal pair $ (f^*, t^*) $ for each dataset, testing variations in $ t^* $ without re-evaluating $ f^* $ would undo the optimization performed and could lead to misleading conclusions. In other words, the threshold is already thoughtfully selected along with the framework, making an additional sensitivity analysis unnecessary.
**T analysis:** Given that sensitivity was a concern across reviewers, we assessed how the number of hard-profiled samples changes when varying the threshold \textit{T}.
To ensure reproducibility, we set a random seed and let NumPy randomly select T from the range (0.05, 0.6) with six distinct values. The Figure in https://anonymous.4open.science/r/icml2025-F9C4/sensitivity_theshold.png illustrates the observed behavior using the smallest and largest datasets from our experiments.
The threshold can be understood as a flexibility level —how much confidence is required before a sample is no longer considered "hard." Lower thresholds allow greater flexibility, meaning the model tolerates lower confidence scores. Given that our predictor is a good generalizer, we observed a few samples with low confidence. As expected, increasing the threshold leads to a higher number of hard samples. However, the change follows a smooth, almost linear trend rather than abrupt shifts.
This indicates that our threshold selection process is reasonable and stable. To enhance clarity in the main paper, we propose explicitly including the optimization equation and adding a section explaining why the chosen \textit{T} is justified. This should benefit both the work and its readers.
**Flipping analysis:** We also assessed how the number of hard-profiled samples changes when varying the threshold or the flipping rate while keeping the other parameter fixed. To ensure reproducibility, we set a random seed and let NumPy randomly select a fixed parameter value from the range (0.05, 0.6), while the variable parameter was chosen from the same range but with six distinct values. The Figure in: https://anonymous.4open.science/r/icml2025-F9C4/sensitivity_threshold_and_flipping.png illustrates the behavior observed. The results show that dataset characteristics significantly influence sensitivity. For the Diabetes dataset, fixing the threshold and varying the noise level leads to considerable changes in the number of hard samples, which is expected given that label flipping in small datasets intuitively affects the data distribution more than in larger ones. However, when fixing the flipping level and varying the threshold, the sensitivity is relatively smooth for both datasets. The curves do not exhibit abrupt changes, confirming that selecting the best threshold for the highest-performing framework remains a reasonable and stable choice. These findings reinforce our original methodology: optimizing $, T^*$ jointly with $f^*$ ensures that the threshold adapts to dataset characteristics without introducing unnecessary complexity or computational overhead.
* **LMM adoption**
We considered using LLM-based methods during the data generation process and actually used GREAT (2023, http://arxiv.org/abs/2210.06280), which exploits an auto-regressive generative LLM to sample synthetic and highly realistic tabular data. However, we did not highlight it separately; instead, we treated it alongside other models. This model was highlighted in Section 5.6, where it demonstrated good potential in replicating low-probability events, with its performance further improved when combined with Profile2Gen. | Summary: The paper introduces Profile2Gen, a novel data-centric framework that generates and refines synthetic data specifically for regression tasks in medical applications. By profiling the original dataset into easy, ambiguous, and hard samples, the framework trains separate generative models and later refines the synthetic data through iterative postprocessing that removes hard samples. Extensive experiments across six public medical datasets—using seven state-of-the-art generative models and evaluating via metrics such as RMSE and Wasserstein distance—demonstrate that Profile2Gen can reduce predictive error and, in some cases, even outperform models trained solely on real data. The authors further extend the DataIQ framework to support regression tasks, making their approach broadly applicable in data-scarce scenarios.
Claims And Evidence: The paper claims that Profile2Gen (1) statistically significantly reduces predictive errors in regression tasks; (2) enhances model reliability and generalization, sometimes achieving comparable or even better performance than real data; (3) preserves minority groups in the data distribution better than traditional methods.
These claims are supported by extensive experiments (approximately 18,000 runs) across multiple datasets and models, with clear quantitative evidence provided via RMSE improvements, Wasserstein distance analyses, and statistical significance tests (e.g., Kruskal-Wallis and Wilcoxon tests). While the evidence is comprehensive, the paper does note some cases where preprocessing alone sometimes outperforms Profile2Gen, indicating that the benefits may vary with dataset/model specifics.
Methods And Evaluation Criteria: The methodological approach is multi-staged: (1) Preprocessing: The original data is profiled (with label flipping used to gauge data quality) to identify easy, ambiguous, and hard samples. (2) Synthetic Data Generation: Generative models are independently trained on these subsets. (3) Postprocessing: The synthetic data is refined by removing hard samples based on a user-defined threshold.
Evaluation is carried out using both the TSTR (Train on Synthetic, Test on Real) protocol and augmentation tasks. Key metrics include RMSE for predictive performance, Wasserstein distance for distribution similarity, and additional analyses of fairness and diversity in the synthetic data. Overall, the chosen methods and criteria are well-aligned to improve data quality for medical regression tasks.
Theoretical Claims: The paper provides theoretical formulations to define “hard” samples via a scoring function and supports the design of the iterative refinement process with derived equations (e.g., Equation 1 for F1 score). Although the derivations appear reasonable, a deeper scrutiny of the proofs would be beneficial—especially to assess the sensitivity of the threshold parameters and their impact on model performance.
Experimental Designs Or Analyses: The experimental design is robust, incorporating: (1) multiple medical datasets (e.g., Parkinson, Urinary, Cholesterol, Body Fat, Plasma, Diabetes) from OpenML; (2) A comprehensive comparison across seven generative models and twelve predictors; (3) Detailed analyses including RMSE plots, distribution comparisons via violin plots, and statistical tests.
One potential concern is the observed variability in performance across datasets—Profile2Gen sometimes lags behind simpler preprocessing approaches. This suggests that further ablation studies or sensitivity analyses (e.g., on the label flipping ratio and threshold T) could provide additional clarity.
Supplementary Material: I reviewed extended methodological descriptions, particularly the adaptation of the DataIQ framework to regression tasks (DataIQReg), with further clarification on the loss functions and uncertainty measures and additional details on the datasets, including preprocessing steps and statistical analyses, which help contextualize the experiments and ensure reproducibility.
Relation To Broader Scientific Literature: The paper situates itself well within the data-centric AI literature by building on recent frameworks such as DataIQ and CleanLab. It also connects with established methods in synthetic data generation (e.g., CTGAN, TVAE) and recent discussions on handling hard samples (e.g., AUM ranking). The discussion could be further enriched by comparing with the latest advances in synthetic data for medical domains.
Essential References Not Discussed: It might benefit from a discussion of recent advances in synthetic data generation using GAN-based methods in medical imaging or other non-tabular data domains. Including such references would provide broader context and help underline the unique contributions of Profile2Gen in a wider landscape of synthetic data research.
Other Strengths And Weaknesses: Strengths:
- Novel integration of data profiling with synthetic data generation for regression tasks.
- Extensive experimental evaluation across diverse datasets and models.
- Practical relevance for overcoming data scarcity in sensitive domains like medicine.
Weaknesses:
- Performance gains are sometimes marginal or inconsistent, depending on the dataset and generative model.
- The framework introduces additional complexity, which may affect reproducibility and requires careful parameter tuning.
- More detailed ablation studies could clarify the influence of key hyperparameters (e.g., threshold T, label flipping ratio).
Other Comments Or Suggestions: - Additional visualizations or error analyses could further illustrate the trade-offs between diversity and generalization in the synthetic data.
- Discussing potential limitations in terms of computational cost and scalability would add value.
- It would be helpful to provide guidelines for selecting optimal thresholds and label flipping ratios.
Questions For Authors: - How sensitive is Profile2Gen to the choice of the threshold T and the label flipping ratio? Have you explored adaptive thresholding methods that could adjust the threshold T dynamically based on dataset characteristics rather than relying on a fixed value?
- Have you explored extensions of Profile2Gen for classification tasks? What modifications would be necessary for such an adaptation?
- Given the variability in performance across different datasets, do you have insights into which characteristics of a dataset favor Profile2Gen over simpler preprocessing methods?
- Can the proposed approach be scaled to higher-dimensional or non-tabular data, and if so, what challenges might arise?
- Could you elaborate on the computational cost and scalability of the framework, especially when handling larger or more complex datasets?
- How does error propagation from the early profiling stage affect the overall performance, and what measures can be taken to mitigate such issues?
- Beyond regression tasks, would this framework apply to other downstream applications such as time-to-event analysis or survival prediction?
- Could you provide further insights into the trade-off between generalization and diversity during the postprocessing stage, and how the method ensures that critical edge-case information is not lost?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: * **Generalization vs. Diversity Trade-off:** Profile2Gen, which incorporates post-processing, reduces Wasserstein's similarity between real and synthetic samples. This indicates that the generated samples are less similar to real data than other techniques. Here is the highlight: the similar samples, which have the same statistical characteristics, are a generalization of the real ones, while the diversity concerns about the samples that are not too similar but follow the distribution patterns ( Alaa et al., 2021, https://arxiv.org/abs/2102.08921). When analyzing the dissimilarity alongside the profile2gen samples and their distributions, we observe that the generated samples are not only different but also diverse while still following the original distribution patterns. The lower similarity indicates that Profile2Gen prioritizes more variable synthetic data, potentially creating a broader range of scenarios and examples. As a consequence, post-processing increases diversity at the cost of generalization since this set of samples is diminished in the synthetic dataset. Higher diversity is generally beneficial in tasks such as data augmentation, where increasing the dataset size does not necessarily improve model performance unless it introduces novel and meaningful variations. However, a lack of generalization may cause the synthetic data distribution to diverge too much from the real data, leading to fidelity loss and getting into the previously discussed by Alaa et al. (2021) trade-off, the diversity-fidelity.
* **Extensions for Other Tasks (Classification, Time-to-Event, etc.) -- Reviwers BQrC (Q2, Q6, Q7), fkDs:**
We appreciate the question about different tasks, and we emphasize that the main difficulty concerns the data-centric framework used to profile the data. We elaborate on our justification:
* **High-dimensional non-tabular data:** Scaling to higher-dimensional or non-tabular data is indeed a relevant challenge. We conducted experiments using time-series data from wearable sensor devices - samples with shape (length, temporal window size, number of sensor axis) - specifically accelerometer data collected. At the same time, subjects performed daily activities such as brushing their teeth, jumping, running, and typing. However, our approach did not yield satisfactory results for this type of data. The main challenges were: 1. The CleanLab framework requires data to be in a tabular format, which is unsuitable for time-series data. 2 In time-series data, the entire temporal window contributes to label determination. Missing or misaligned steps could alter labels — for example, distinguishing running from jogging became problematic. Even when we added a datetime column to better structure the data, the approach still failed. 3. We tested the approach using DataIQTorch - from DataIQ - which allowed us to bypass the tabular conversion issue. However, obtaining confidence scores through the framework's methods was not straightforward, leading to inconsistencies.
Developing a version of these frameworks specifically designed for time-series data could help address these challenges. However, despite several attempts, the effort required to adapt the existing framework for non-tabular data did not justify the results obtained. As a result, we decided not to pursue this direction further within the scope of our study.
* **Classification tasks:** A similar technique developed by Hansel et al. (2023, https://arxiv.org/pdf/2310.16981 ) addresses classification tasks. However, existing approaches still lack extensive exploration regarding generative regression-focused tasks. Our work aims to fill this gap by highlighting its limitations and the need for further research in this field, which also inspired us to adapt the method for regression tasks.
To achieve this, it was necessary to modify DataIQ to support regression, as we did in our approach. Additionally, performance metrics determined our framework selection entirely, whereas Hansel et al. (2023) incorporated additional aspects and limitations beyond purely metric-based decisions.
* **Time-to-event and other tasks:** We believe that the core of the framework —preprocessing, profiling samples, and following the remaining workflow — can be applied to time-to-event analysis and survival prediction. However, the current profiling frameworks (Cleanlab and DataIQ Reg) are not properly designed to handle survival data. Specifically, the concept of hard samples in survival analysis must account for censorship and the nature of time-to-event data, not just the confidence level of the models, which these frameworks do not consider. If a DataIQ Survival framework were developed to address these limitations, we strongly believe that Profile2Gen would be a suitable approach for synthetic data generation in survival analysis.
**Please review the response provided to reviewers sXia and fkDs, where we address your concern.** | Summary: This paper introduces Profile2Gen, a data-centric framework designed to enhance the generation and refinement of synthetic data for medical regression tasks. The key innovation lies in profiling and addressing hard-to-learn samples, which traditionally hinder model performance and generalization. The authors evaluate their approach across six medical datasets using seven state-of-the-art generative models and conduct experiments to validate its efficacy.
Claims And Evidence: Generally well-supported. For instance, Profile2Gen reduces variability across random seeds and datasets. The authors provide statistical significance tests (Wilcoxon and Kruskal-Wallis) to validate this. This well-supports that ofile2Gen improves consistency and robustness in model performance.
Methods And Evaluation Criteria: The methods and evaluation criteria are ok.
Strengths:
1. Benchmarking on multiple datasets strengthens the validity of the claims.
2. Rigorous statistical testing (Wilcoxon, Kruskal-Wallis) improves credibility.
Weaknesses:
3. Hyperparameter Sensitivity: The choice of hard sample thresholds is not deeply analyzed.
4. Scalability Concerns: The computational cost of profiling large datasets is not discussed in detail.
Theoretical Claims: No theory.
Experimental Designs Or Analyses: Yes, the experiments are well-designed with:
1. Multiple evaluation protocols (TSTR, augmentation)
2. Diverse datasets (six medical datasets)
3. Multiple generative models (CTGAN, TVAE, Bayesian Network, etc.)
4. Twelve predictive models evaluated via AutoGluon
Concerns:
Synthetic Data Proportions: The results show that adding 68.2% synthetic data degrades performance, but the exact reason is not deeply analyzed.
Model-Specific Performance: Some generative models (e.g., CTGAN) show high variability, but the authors do not discuss why.
Supplementary Material: I glanced at the supplementary material.
Relation To Broader Scientific Literature: Synthetic data are generally very important in scientific discoveries.
Essential References Not Discussed: NA.
Other Strengths And Weaknesses: Strengths:
1. Comprehensive experiments (18,000 trials).
2. Fairness-aware synthetic data generation.
3.Robust statistical evaluation (Wilcoxon test).
4. Profile2Gen generalizes well across datasets.
Weaknesses:
1. No deep theoretical justification for removing hard samples.
2. Hyperparameter sensitivity (thresholds for hard sample removal).
3. Scalability concerns for large datasets.
Other Comments Or Suggestions: NA.
Questions For Authors: NA.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear reviewers:
We want to thank you all for your very careful and thoughtful reviews. We were very encouraged by the numerous and significant strengths that you all identified in our study. Namely:
* An innovative data-centric approach integrating data profiling and synthetic data generation targeting hard-to-learn samples in regression tasks.
* Extensive empirical validation with approximately 18,000 rigorous experiments across 6 medical datasets, 7 SOTA generative models, and 12 predictive models.
* We use a rigorous statistical approach in our comparisons. 4. Extending the widely recognized DataIQ framework from classification to regression tasks, enabling comprehensive profiling and data quality assessment in regression contexts.
* Reduces model performance variability across random seeds and datasets, consistently outperforming traditional and baseline preprocessing methods.
* Preserves minority distributions, crucial for accurately capturing rare and critical medical scenarios.
* Clear potential for real-world deployment in data-scarce or privacy-sensitive medical applications.
We appreciate your thorough identification of potential steps to address the study’s weaknesses. Due to space constraints, we have grouped our responses by topic.
Thus, we hope to be given the chance to address those weaknesses in a revision. We eagerly await your answers.
Sincerely, --the authors
* **Scalability Concerns e Computational Cost -- Reviwers sXia, BQrC (Q5), VmCi (Q3)**
To assess computational efficiency, we selected the largest dataset, Parkinson’s, which contains approximately 3,500 training samples. We applied the framework selection process (Cleanlab and DataIQ) along with profiling, using two thresholds and a label replacement ratio. These experiments required 3,510 MB of memory and took approximately 3 minutes.
For larger datasets, it is important to consider that memory usage will increase proportionally, as observed in the profiling stage. However, it should be noted that the process itself does not require GPU resources. Memory remains the main concern at this stage. For generating synthetic samples, particularly for Transformer and LLM-based models, we utilized an Nvidia RTX4090.
When working with datasets larger than 3,500 samples, memory consumption could be calculated based on this scaling factor, considering the amount of data processed. While simulating this for larger datasets may be difficult, this scaling factor can provide a reasonable estimate. It is worth noting that finding large datasets, especially in healthcare, is challenging, and generating synthetic data is particularly relevant in scarcity scenarios where such large datasets are not readily available.
To ensure clarity and transparency, we could create a section in the supplementary materials to further detail the memory usage and computational considerations. In the main paper, we could then explicitly mention this section, where we discuss memory usage in more depth, offering readers more context on how the scaling might work for larger datasets.
Hard removal: Hard-to-learn samples (hard) can negatively impact model performance by either:
Increasing uncertainty in predictions. The model may predict correctly but with low confidence, leading to unreliable decision-making.
Reinforcing incorrect patterns. The model may misclassify these samples with high confidence, making it more prone to overfitting on noise rather than learning meaningful patterns.
* **Hard removal -- Reviewer sXia**
Removing these samples is a well-established machine learning technique, often called dataset cleansing or data curation. Studies have shown that filtering out mislabeled or overly ambiguous samples can improve model generalization (https://arxiv.org/abs/1911.00068, https://arxiv.org/abs/2310.16981).
Formally, let $ X = X_{\text{easy}} \cup X_{\text{hard}} $ be the dataset, where $ X_{\text{easy}} $ are well-confident samples, and $ X_{\text{hard}} $ are ambiguous or mislabeled samples. The model’s expected loss can be decomposed as:
\begin{equation}
\mathbb{E}[\mathcal{L}(X)] = \mathbb{E}[\mathcal{L}(X_{\text{easy}})] + \mathbb{E}[\mathcal{L}(X_{\text{hard}})].
\end{equation}
Since $ X_{\text{hard}} $ contributes disproportionately to loss without meaningful learning, its removal reduces noise and enhances generalization. Empirically, prior works on curriculum learning (https://ronan.collobert.com/pub/2009_curriculum_icml.pdf) } and label noise filtering (https://arxiv.org/pdf/1712.05055) support this approach, demonstrating that excluding ambiguous samples can lead to more robust models.
To avoid confusion, we will refine the introduction (where we commented about these samples) to emphasize that hard sample removal is not an arbitrary step but a widely used strategy for improving model robustness.
**Please review the response provided to reviewers BQrC, fkDs, and VmCi, where we address your concern.** | null | null | null | null | null | null |
KIND: Knowledge Integration and Diversion for Training Decomposable Models | Accept (poster) | Summary: This paper tårgets on training a better pre-trained model for downstream tasks. Concretely, they propose KIND (Knowledge Integration and Diversion). It utilizes SVD to yield basic components, and then classify them into two categories, learngenes and tailors. The former captures class-agnostic features, while the latter captures class-specific ones. With SVD, it trains basic components instead of the full-weight matrices. This method is reported to be the first to apply learngenes to image generation tasks. They establish a benchmark for evaluating the transferability of diffusion models. Extensive reported results prove the effectiveness of the proposed method.
## After Rebuttal
After reading the rebuttal and other reviews, I still tend to accept this paper.
Claims And Evidence: One key idea in this method is to adopt SVD to categorize basic components into learngenes and tailors. This claim can be supported by previous works that SVD has been applied to disentangle class-agnostic and class-specific components.
Methods And Evaluation Criteria: I think the method is reasonable and new to me. Previous methods have applied SVD, but this method also shows enough novelty to me.
I think the benchmark datasets cover some basic datasets in image generation, and plenty of criteria and scenarios have been incorporated in the experiment section.
Theoretical Claims: I have checked A3. I have read A2 but I am not familiar with DK Theorem.
Experimental Designs Or Analyses: I think the experiment section in this paper is good. It covers multiple datasets and settings, and reports enough criteria to validate the performance of methods. I think constructing such benchmark is beneficial to the community.
Supplementary Material: I have reviewed the appendix, including theoretic insights, more descriptions of datasets, and more generation results.
Relation To Broader Scientific Literature: I think this is an interesting paper. Besides the interesting method proposed in this paper, the benchmark they construct might be meaningful.
Essential References Not Discussed: N/A from my perspective.
Other Strengths And Weaknesses: The figures in this paper are good, illustrating the idea in a clear manner.
Other Comments Or Suggestions: N/A
Questions For Authors: I want to see more discussions on the limitations of the proposed method. Some failure cases are also welcome.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer Dcjo,
We sincerely appreciate your insightful comments and your recognition of both the novelty and soundness of our methods, as well as the contribution of our benchmark to the community. Below, we provide a detailed response.
>**Q1: Discussions on the limitations of the proposed method.**
We have briefly discussed the limitations in Section 7 of the original manuscript. Here, we further elaborate on these limitations and outline potential directions for future improvements:
- **Limitations in Class-Conditional Generation.**
To illustrate the transferability of class-agnostic knowledge obtained via knowledge diversion, we focus on class-conditional generation tasks, where variations induced by different class labels naturally introduce downstream tasks with substantial domain shifts.
In contrast, text-conditional generation, which controls image content via prompts, is also widely adopted.
However, large-scale text-to-image diffusion models (e.g., Stable Diffusion 3) are pre-trained on a broad spectrum of internet images, making it challenging to define tasks with significant domain shifts.
Moreover, extending KIND to text-conditional generation requires transitioning class gate from discrete, countable class labels to an open-ended, uncountable prompt space, where **a binary class gate is insufficient**.
Future work will explore Mixture-of-Experts (MoE) techniques for knowledge diversion, enabling dynamic allocation of a limited set of tailors based on prompts.
We have conduct preliminary experiments using a PixArt-based model trained for 50,000 steps, see Tabel below. KIND may underperform compared to parameter-efficient fine-tuning (PEFT) methods such as LoRA, as pre-trained text-to-image diffusion models inherently bridge moderate domain differences.
|Dataset: MRI| CLIP Score↑|LPIPS↓
|-|-|-
|PixArt-Lora|**33.88**| 0.4252
|PixArt-KIND|33.20|**0.4213**
|Dataset: Pokemon|CLIP Score↑|LPIPS↓
|-|-|-
|PixArt-Lora|32.48|**0.4279**
|PixArt-KIND|**32.55**|0.4288
- **Limitations in Structural Expansion.**
KIND has been applied exclusively to Transformer-based architectures, focusing on knowledge diversion in Multi-Head Self-Attention ($W_q$, $W_k$, $W_v$, $W_o$) and Pointwise Feedforward layers ($W_{in}$, $W_{out}$).
While DiT is becoming the dominant architecture for diffusion models, many classic diffusion models still rely on convolution-based UNets.
Extending KIND to architectures dominated by convolutional layers presents a key challenge.
Although convolutional weights can be represented as three-dimensional tensors and prior work has explored SVD-based decomposition for convolutional layers, the strong inductive biases of convolutional kernels pose unique difficulties.
Developing effective knowledge diversion strategies for convolutional networks remains an important direction for future research.
- **Limitations in Other Tasks (e.g., Image Classification).**
KIND has been primarily evaluated on image generation tasks, yet its knowledge diversion mechanism—encapsulating class-agnostic and class-specific knowledge into distinct network components—suggests broader applicability.
A particularly promising direction is cross-domain few-shot learning, where models must generalize across domains with limited data. Traditional methods often struggle under large distribution shifts due to their reliance on prior knowledge from the source domain.
KIND offers a key advantage: learngenes serve as a transferable backbone for stable adaptation, while tailors enable task-specific fine-tuning with minimal data, improving generalization.
However, unlike image generation, image classification lacks access to class labels during inference, requiring each image to traverse all tailors to extract features, leading to increased computational overhead. As the number of classes grows, classification complexity further escalates.
Preliminary experiments applying KIND to ViT for cross-domain few-shot learning (see Tabel below) demonstrate significant improvements over baselines, though a performance gap remains compared to state-of-the-art methods. Thus, developing an efficient learngene-tailer framework for classification remains an open research direction.
||ChestX|ISIC|EuroSAT|CropDisease|Average
|-|-|-|-|-|-
|Vanilla ViT (Baseline)|26.3|46.1|88.6|94.6|63.9
|P>M>F|**27.3**|50.1|86.0|93.0|64.1
|StyleAdv|27.0|**51.2**|**90.1**|**96.0**|**66.1**
|KIND|26.5|47.9|88.8|95.0|64.6
We will provide a detailed discussion of these limitations and future research directions in the revised Appendix to inspire further advancements in KIND and broaden its application scope.
---
Rebuttal Comment 1.1:
Comment: After reading the rebuttal, most of my concerns are solved. I still tend to accept this paper. | Summary: This manuscript proposes a novel pre-training method named KIND, aiming to address the adaptability issues of traditional pre-trained models in different tasks and deployment scenarios. KIND integrates and distributes knowledge by using SVD during the pre-training process, creating learngenes and tailors respectively, and achieves effective knowledge transfer through a class gate mechanism. Experiments verify that KIND can be flexibly deployed in various scenarios and significantly improve the transfer efficiency in tasks with large domain shifts. The contribution of KIND lies in providing a decomposable structure for pre-trained models, enabling the models to be dynamically adjusted according to task requirements.
## update after rebuttal
The author's response has addressed my concerns, and I am inclined to accept this paper.
Claims And Evidence: The authors analyzed the existing problems and put forward the claim of "rethinking the pre-training process to develop decomposable pre-trained models".
Methods And Evaluation Criteria: The method is applicable to solving the problem of model decomposition, and the experimental verification indicators are reasonable.
Theoretical Claims: The core theory is based on SVD, which is relatively easy to understand.
Experimental Designs Or Analyses: The experimental design is reliable, and the datasets used in the experiments include ImageNet and several downstream datasets.
Supplementary Material: The supplementary material contains the code, which I have reviewed. It is recommended that the authors add a README file to the code.
Relation To Broader Scientific Literature: The core decomposition method of this paper is quite similar to that of the paper "FacT: Factor-Tuning for Lightweight Adaptation on Vision Transformer" published in AAAI 2023, but no discussion is carried out.
Essential References Not Discussed: The core decomposition method of this paper is quite similar to that of the paper "FacT: Factor-Tuning for Lightweight Adaptation on Vision Transformer" published in AAAI 2023, but the authors did not conduct a comparison and discussion. In addition, the paper "PARAMETER-EFFICIENT ORTHOGONAL FINETUNING VIA BUTTERFLY FACTORIZATION" published in ICLR 2024 should also be compared and discussed.
Other Strengths And Weaknesses: Strengths
1 The overall writing logic is relatively clear.
2 The feature of "no further time-consuming steps required" is very friendly to the environment with limited computing resources.
Weaknesses
1 There is a lack of comparison and discussion of the decomposition methods in FacT of AAAI 2023 and BOFT of ICLR 2024.
2 One of the authors' core arguments is the application in the Limited Resources scenario, but this point is not highlighted in the experimental part. For example, it is recommended to add experiments on mobile devices.
Other Comments Or Suggestions: It is recommended to introduce a README part in the code of the supplementary material, otherwise it will cause inconvenience for reviewers to review.
Questions For Authors: The authors compared the number of parameters and the amount of computation in Table 2. It is recommended to supplement the comparison of speed.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer Y7yt,
We sincerely appreciate your insightful feedback and your recognition of the innovation and practicality of our work. Below, we provide our detailed response.
>**Q1: Lack of comparison of similar methods (e.g., FacT and BOFT).**
FacT and BOFT leverage matrix decomposition techniques relevant to this work but are fundamentally Parameter-Efficient Fine-Tuning (PEFT) methods.
They focus on decomposing pre-trained weight matrices to identify compact parameter subspaces, that can be efficiently fine-tuned for adapting pre-trained models to novel tasks. However, these methods heavily rely on traditional pre-trained models, which are typically fixed in size, structurally inflexible, and risk negative transfer.
In contrast, KIND introduces **a novel pre-training paradigm** that explicitly decomposes knowledge into class-agnostic and class-specific components, encapsulated in learngenes and tailors, respectively. This approach results in decomposable pre-trained models, where the modular design enhances transferability while enabling task-specific adaptation, effectively addressing the limitations of traditional pre-training.
Table 2 in the manuscript highlights the superior transferability of learngenes by comparing KIND with PEFT-based methods, including SVD-based approaches (e.g., SVDiff, PiSSA) related to FacT, and OFT-based methods related to BOFT.
Per your suggestion, additional comparisons with FacT and BOFT (see Table below) further demonstrate that KIND consistently outperforms these PEFT methods, underscoring its ability to transfer only class-agnostic knowledge while avoiding the deployment challenges and the redundant, biased, or harmful transfer often associated with traditional pre-trained models on which PEFT approaches typically rely.
|DiT-B|CelebA|Hubble|MRI|Pokemon
|-|-|-|-|-|
|FacT-TT|0.307|0.242|0.067|0.425
|BOFT|0.318|0.247|0.058|0.433
|KIND|**0.201**|**0.124**|**0.042**|**0.343**
|DiT-L|CelebA|Hubble|MRI|Pokemon
|-|-|-|-|-|
|FacT-TT|0.240|0.168|0.081|0.299
|BOFT|0.213|0.155|0.051|0.296
|KIND|**0.152**|**0.109**|**0.040**|**0.262**
>**Q2: Application in the limited resources scenario is not highlighted in experiments.**
The decomposable model pre-trained by KIND can be flexibly restructured to accommodate computational constraints, enabling efficient deployment on **mobile and edge devices**.
Although direct evaluation on mobile hardware is beyond our current resources, we approximate its feasibility by analyzing FLOPs, memory footprint, and extrapolating inference latency on modern mobile chip.
We construct a mobile-compatible DiT using KIND and evaluate its efficiency across three state-of-the-art mobile chip: Apple A18, Kirin 9020, and Snapdragon 8 Gen3, which sustain 1907, 1720 and 2774 GFLOPS, respectively.
As shown in Table below, KIND-Mobile achieves a 3.3$\times$ reduction in FLOPs and a 1.8$\times$ reduction in memory usage compared to traditional pre-training, while maintaining strong generative performance (FID=21.14).
Notably, inference latency remains under 4 seconds across all tested mobile chip, demonstrating KIND’s adaptability in resource-constrained environments.
||Param.|FLOPs (G)|Memory (MB)|Apple A18 (s)|Kirin 9020 (s)|Snapdragon 8 Gen3 (s)|FID↓|IS↑
|-|-|-|-|-|-|-|-|-
|Traditional PT|129.7|43.62|518.8|11.43|12.68|7.86|25.14|47.15
|KIND-Mobile|**70.2**|**13.22**|**280.8**|**3.47**|**3.84**|**2.38**|**21.14**|**58.18**
>**Q3: Supplement the comparison of speed in Table 2.**
To further emphasize the computational efficiency of KIND on novel tasks, we report the GPU time of different methods in the Table below, following your suggestion.
KIND achieves the best performance with the most efficient training compared with state-of-the-art PEFT methods. This is attributed to its encapsulation of class-agnostic knowledge into learngenes through knowledge diversion, thus enhancing structural flexibility.Notably, under large domain shifts, transferring only learngenes improves the adaptability of the pre-trained model while significantly enhancing transfer efficiency by reducing model parameters through the elimination of redundant class-specific knowledge encapsulated in tailors.
|DiT-B|Para.|FLOPs|GPU Time
|-|-|-|-
|SVDiff|**0.1**|43.6|2.5
|OFT|14.2|119.7|6.6
|LoRA|12.8|50.1|2.9
|PiSSA|12.8|50.1|2.9
|LoHa|12.7|87.1|3.9
|DoRA|12.8|129.5|6.2
|Heur-LG|129.6|43.6|4.89
|Auto-LG|129.6|43.6|4.89
|Full FT|129.6|43.6|4.89
|KIND|12.8|**33.7**|**1.6**
|DiT-L|Para.|FLOPs|GPU Time|
|-|-|-|-
|SVDiff|**0.2**|155.0|6.6|
|OFT|50.5|425.6|14.2|
|LoRA|45.3|178.2|7.1|
|PiSSA|45.3|178.2|7.1|
|LoHa|45.3|309.6|12.8|
|DoRA|45.6|503.0|22.2|
|Heur-LG|456.8|155.0|10.0|
|Auto-LG|456.8|155.0|10.0|
|Full FT|456.8|155.0|10.0|
|KIND|45.4|**119.6**|**6.3**|
>**Q4: Introduce a README part in the code.**
Thank you for your suggestion. We will include a comprehensive README file in the future open-source release to facilitate the reproduction of KIND.
---
Rebuttal Comment 1.1:
Comment: Thank you for the author's reply, which has addressed most of my concerns. The author has added a comparison with similar methods and conducted additional experiments in the mobile scenario.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer Y7yt,
We sincerely appreciate your positive evaluation of our manuscript and your insightful comments. Your detailed feedback has been invaluable in refining our work.
If there are any remaining concerns, we would be happy to engage in further discussion. Thank you for your time and thoughtful review.
Best regards. | Summary: ## Summary
This work applies SVD on the weight matrices $W_q, W_k, W_v, W_o, W_{in}, W_{out}$ of pretrained diffusion transformers (DITs). Then finetunes the SVD decomposed matrices U, $\Sigma, $V$ with target label information. The SVD decomposed matrices are futher splited into two parts to store 1) general information and 2) target label specified information.
## strongthness
- The idea of pretraining DiTs with SVD decomposition of weights is interesting.
- The reconstruction quality of DiTs trained by the proposed method is clearly better than that of other methods. (e.g. Figure 4, 5).
## weakness
- Although the proposed method appears simple (as shown in Algorithm 1), the writing is somewhat hard to follow. I am confused about this paper. For example, line 123 "KIND decomposes pre-trained models" implies applying KIND after pretraining. However, the learning of learngenes and tailors (line 217) requires applying KIND during pretraining. Again, Table 1, 2, 3 compares KIND with other "post-training" methods, while line 251, section 5.1 says "the model pretrained by KIND".
Where does the KIND apply, pretraining or post-training? and What do you want to compare with, pretraining approaches or post-training approaches?
- Assuming KIND is applied on model pretraining (line 251, section 5.1), did other post-training methods in table 1,2,3 use the KIND pretrained DiTs? or normally pretrained DiTs? Keep in mind that, KIND pretraining benefits from the target label information. Did normally pretrained DiTs, if there is any, use the target label information.
- Without a clarification about the concerns above, the fairness of experimental results is questionable.
## suggestions
- I suggest author to put Algorithm 1 in the main text to make the paper easy to understand. As a reader of an experimental work, I want to know 1) How does the algorithm work (algorithm 1) and 2) What are the results. The Algorithm 1 is so clear and so simple! It should be in the main text.
- Line 150~155 shows the SVD reparameterization is applized on $W_q, W_k, W_v, W_o, W_{in}, W_{out}$. However, Figure 2 implies that the SVD is only applied on $W_{in}, W_{out}$. I suggest to update figure 2 accordingly.
- I am positive on this paper because of the interesting reconstruction quality. However, it is important to have a fair comparison and a clear expression.
### questions
- Algorithm 1 line 1 sayes the initialization of both W and SVD matrices U, $\Sigma$, V. Did you use both matrices, or one? I am confused. It seems that Algorithm 1 line 8 uses SVD matrices U, $\Sigma$, V, rather than W. If this is the case, how do you constrain $U^{\top}U=I$?
Claims And Evidence: check summary
Methods And Evaluation Criteria: check summary
Theoretical Claims: no theory.
Experimental Designs Or Analyses: yes.
Supplementary Material: yes.
Relation To Broader Scientific Literature: check summary
Essential References Not Discussed: no.
Other Strengths And Weaknesses: check summary
Other Comments Or Suggestions: check summary
Questions For Authors: check summary
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer QbMr,
We sincerely appreciate your valuable comments and recognition of our work’s innovation and performance. Below is our detailed response.
>**Q1: Where does the KIND apply, pretraining or post-training? What do you want to compare with, pretraining approaches or post-training approaches?**
KIND is a novel pre-training method for constructing decomposable models. Unlike traditional pre-training approaches, KIND explicitly partitions knowledge into class-agnostic and class-specific components, encapsulating them in learngenes and tailors, respectively.
This decomposition transforms fixed-size models into modular structures, where learngenes enhance transferability, and tailors adapt to specific tasks.
KIND operates during pre-training, producing learngenes and tailors for flexible downstream deployment.
Accordingly, we first compare it with pre-training methods such as traditional PT and Laptop-Diff, demonstrating that training a decomposable model incurs no extra computational cost while improving structural flexibility.
To highlight the strong transferability of class-agnostic knowledge, we also compare it with parameter-efficient fine-tuning methods (i.e., post-training approaches) such as LoRA and PiSSA, particularly in tasks with large domain shifts.
In summary, KIND is a pre-training framework that enhances post-training adaptability by enabling adaptive model scaling based on task demands and computational resources.
>**Q2: Did other post-training methods in Table 1,2,3 use the KIND pretrained DiTs or normally pretrained DiTs? Did normally pretrained DiTs use the target label information?**
As noted in Q1, KIND is a pre-training framework for decomposable models that enhances post-training flexibility.
Table 1 compares different pre-training strategies, including traditional PT and knowledge distillation (e.g., Laptop-Diff), in constructing models of various sizes.
In contrast, Tables 2 and 3 evaluate downstream performance, comparing KIND with parameter-efficient fine-tuning methods applied to **normally pretrained DiTs**.
This setup ensures a fair comparison, as normally pretrained DiTs also incorporate target label information.
Normally pretrained DiTs generate images based on class-conditioned information and inherently depend on class labels during pre-training.
To further validate fairness, we compare the training performance of KIND-pretrained models with normally pretrained models (see Table below).
The results confirm that normally pretrained models perform comparably to KIND, demonstrating that improvements in Tables 2 and 3 solely stem from the class-agnostic knowledge encapsulated in learngenes.
||Model|Steps|FID↓|sFID↓|IS↑|Prec.↑|Rec.↑
|-|-|-|-|-|-|-|-
|Traditional PT|DiT-L|300K|9.68|**6.15**|72.22|0.69|**0.47**
|KIND|DiT-L|300K|**9.33**|6.80|**79.39**|0.69|0.46
>**Q3: Fairness of experimental results.**
We have addressed your concerns in detail in Q1 and Q2, which we believe sufficiently clarify this issue.
>**Q4: Algorithm 1 line 1 says the initialization of both $W$ and SVD matrices $U$, $\Sigma$, $V$. Did you use both matrices, or one? How do you constrain $U^\top U=I$?**
We apologize for any confusion caused by the imprecise wording in Algorithm 1, line 1.
As you noted, during knowledge diversion, gradient updates are applied only to $U$, $\Sigma$ and $V$, while $W$ is indirectly updated via Eq. (5) as $W=U\Sigma V^\top$.
Regarding the constraint $U^\top U=I$, we initially explored enforcing orthogonality using **Cayley parameterization** (details can be found in official PyTorch documentation), a transformation that maps a skew-symmetric matrix to an orthogonal matrix.
Specifically, we can construct $U$ as $U=(I+Q)(I-Q)^{-1}$, where $Q$ is a skew-symmetric matrix satisfying $Q=-Q^\top$.
While this guarantees orthogonality, it incurs substantial computational overhead ($\sim7\times$, see table below) due to the matrix inversion, without notable empirical benefits.
||Model|Steps|GPU Time|FID↓|sFID↓|IS↑|Prec.↑|Rec.↑
|-|-|-|-|-|-|-|-|-
|w/ Cayley|DiT-B/4|200K|104.8 hour|56.99|**47.04**|24.7|0.38|**0.46**
|w/o Cayley|DiT-B/4|200K|14.7 hour|**52.78**|49.66|**25.7**|**0.40**|0.45
Given these trade-offs, we do not enforce explicit orthogonality constraints. Instead, we employ class gates to associate distinct feature representations with corresponding singular vectors, thereby naturally mitigating correlations among the singular vectors. This enables $U$ and $V$ to approximate orthogonality through the learning process.
As shown in [Figure](https://anonymous.4open.science/api/repo/a-8112/file/12.pdf), the process of knowledge diversion through class gate allows the learned matrices to preserve orthogonality without requiring explicit constraints.
>**Q5: Other suggestions.**
Thank you for your valuable suggestion. We will move Algorithm 1 to the main text and complete the missing details in Figure 2 in revision. | Summary: This paper proposes a method to decompose a model’s learnable matrices into class-agnostic knowledge (learngenes) and class-specific knowledge (tailors) using Singular Value Decomposition (SVD). The learning process for tailors is regulated by a class gate, ensuring that only one class is activated per image. After training, the decomposed components can be flexibly recombined based on specific downstream tasks and resource constraints by selecting the required tailors.
The authors conduct experiments using a generative DiT model to demonstrate a better trade-off between the number of training parameters and generation quality. Additionally, the proposed method improves knowledge transferability to novel classes and datasets with larger domain shifts.
Claims And Evidence: • The claimed benefit of reduced training complexity (Lines 257–258) lacks sufficient experimental support. If training classes are isolated using the class gate, does this introduce sparse gradients, potentially making the training process more challenging?
• The claim that learngenes capture task-agnostic information is not well supported by the visualization in Figure 7. The generated images from learngenes exhibit recognizable object-like patterns, and different seeds produce distinct patterns. This observation contradicts the assertion that learngenes do not favor any specific class. Further clarification or empirical validation is needed to reconcile this discrepancy.
• The extent of class-agnostic information varies across different classes. For example, fur may be considered class-agnostic when training involves only cats and dogs, but this assumption may not hold in a more diverse dataset. This suggests that the knowledge encoded in learngenes is highly dependent on the specific combination of training classes. This dependency should be explicitly discussed.
• While learngenes are expected to be transferable across different domains, the exact nature of the transferred knowledge remains unclear. The paper does not provide a thorough validation of what aspects of knowledge are being effectively transferred. Additional experiments or analysis would help substantiate this claim.
• A cross-class validation is missing to support the claim that tailors are class-dependent. For instance, what happens if the tailors from class A are used to generate images for class B? Including such an experiment would help confirm whether tailors truly capture class-specific information and whether their utility is restricted to the classes they were trained on.
Methods And Evaluation Criteria: See the Claims And Evidence session.
Theoretical Claims: The core assumption in Line 636 states that the learned weight is close to an underlying matrix and that the matrix decomposition holds when perturbations are sufficiently small. How can this assumption be systematically evaluated across different scenarios? In tasks with larger domain gaps, the distinction between learngenes and tailors becomes more pronounced. How can this difference be quantified to ensure that the assumption remains valid? Providing empirical or theoretical justification for this assumption across varying domain shifts would strengthen the paper’s argument.
Experimental Designs Or Analyses: • What happens when training with a significantly larger number of classes? Since the parameter size is directly linked to the size of tailors, as shown in Table 1, will the model expand and scale linearly? If so, does this suggest that the proposed method’s efficiency gains diminish as the number of classes increases? Clarifying the scalability of the approach would strengthen the discussion.
• The details for Table 5 are missing. Additional explanations regarding the setup, evaluation metrics, and key findings should be provided to ensure clarity and completeness.
Supplementary Material: The supplementary material contains code only, which I had a look.
Relation To Broader Scientific Literature: The key contributions are related to knowledge decomposition, parameter decomposition, and recombination. They might also relate to research areas such as domain shift and model personalization.
Essential References Not Discussed: The authors are encouraged to discuss some related papers in the area of NAS, which train one model but can be regrouped at no cost at inference [A]
[A] Once-for-All: Train One Network and Specialize it for Efficient Deployment. ICLR'20.
Other Strengths And Weaknesses: see previous sessions.
Other Comments Or Suggestions: N/A
Questions For Authors: • For tasks involving novel classes, how is the tailor initialized? Is the entire tailor randomly initialized, or only a portion of it? It is assumed that each task begins with an initialized tailor, but since different tasks involve varying numbers of classes, does this imply that the model size is variable? The parameter values reported in Table 2 appear to be fixed, clarification on this aspect is needed.
• Is there a direct relationship between the number of training parameters and FLOPS? If so, providing explicit details or empirical validation would strengthen the discussion.
• What is the exact improvement of KIND over FT in Table 3? Reporting the numerical difference would make the performance comparison more precise and informative.
• Can this method generate combinations of multiple classes? If so, how is the combination controlled or influenced by the tailors? If not, what are the key limitations preventing such functionality?
• How are closely related tailors selected for fine-tuning, as described in Line 217? What is the selection criterion, and how many tailors are chosen for fine-tuning? A more detailed explanation of this process would improve clarity and reproducibility.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer abHL,
We sincerely appreciate your recognition of our practicality and efficiency.
Due to length constraints, **experimental tables and figures, are provided via anonymous links (permitted by ICML25)**.
>**Q1:Class Gate and Sparse Gradients**
Parameter updates remain sufficient without excessive sparsity (see [Table](https://anonymous.4open.science/api/repo/a-8112/file/1.pdf)). The learngene, shared across all classes, receives updates from all samples, while tailors benefit from batch training, ensuring broad class coverage (batch size=256, total classes=150).
This setup also reduces gradient conflicts across classes, allowing KIND to achieve competitive performance with similar overhead while maintaining a flexible, decomposable structure.
>**Q2:Task-agnostic Knowledge in Learngenes**
Figure 7 shows that images generated solely from learngenes lack class-specific semantics (visually similar regardless of input labels under the same seed).
To quantify this, [Table](https://anonymous.4open.science/api/repo/a-8112/file/2.pdf) (i.e., Table 5) analyzes the classification distributions of InceptionNet across raw ImageNet images, pre-trained model outputs, learngene-generated images, and pure noise. Entropy, variance, and kurtosis are used to measure distribution uniformity, discreteness, and sharpness.
Results show that learngene-generated images exhibit low correlation with all ImageNet classes and align statistically closer to noise, confirming their class-agnostic nature and lack of semantics.
>**Q3:Specific Combinations of Training Class**
This concern arises only with extremely limited classes, e.g., shared features like fur may dominate between cats and dogs, but introducing a distinct class, such as turtles, reduces this effect.
[Tabel](https://anonymous.4open.science/api/repo/a-8112/file/3.pdf) shows that beyond 100 classes, additional classes offer minimal benefit. As long as the class set is sufficiently diverse, its specific composition has little impact.
>**Q4:Nature of Transferred Knowledge**
BLIP-based VQA verification in [Tabel](https://anonymous.4open.science/api/repo/a-8112/file/4.pdf) confirms that learngene-generated images are natural images (only 5.1\% are classified as 'noisy images').
This suggests that learngenes encode a general noise-to-image mapping, while tailors inject class semantics.
>**Q5:Cross-class Validation**
As shown in [Figure](https://anonymous.4open.science/api/repo/a-8112/file/5.pdf), the 'panda' tailor fails to generate images for other classes, confirming its class-specific nature.
>**Q6: Theoretical Assumptions**
The core assumption holds under large domain shifts.
Frobenius norm in [Tabel](https://anonymous.4open.science/api/repo/a-8112/file/6.pdf) shows minimal weight perturbations ($||E^{[t]}||\ll||W^*||$) when transferring learngenes across domains.
>**Q7:Larger Number of Classes**
A larger number of training classes is unnecessary, as 100 classes is sufficient for capturing class-agnostic knowledge (see Q3).
Once the class-agnostic knowledge has encapsulated in learngenes, additional classes can be integrated by training only corresponding tailors.
>**Q8:Missing Details for Table 5**
See Q2.
>**Q9:Related Works in NAS**
Both KIND and NAS support variable-sized models, but only KIND extracts class-agnostic knowledge for transferability, while NAS focuses solely on network structure.
[Tabel](https://anonymous.4open.science/api/repo/a-8112/file/7.pdf) shows that NAS struggles with domain shifts.
>**Q10:Tailor Initialization and Model Size**
In new tasks, the tailor is typically randomly initialized, which is simple and effective (see Q14).
The number of tailors and parameters varies with class count, with Table 2 reporting the **average parameters** across tasks.
Model size is also influenced by task complexity, and adjusting each tailor's rank balances performance and efficiency (see [Tabel](https://anonymous.4open.science/api/repo/a-8112/file/8.pdf)).
>**Q11:Relationship between Parameters and FLOPs**
Training parameters and FLOPs are related but not strictly proportional, as FLOPs depend on both parameter count and computational patterns like matrix multiplications.
>**Q12:Performance Gains over FT**
We further compare full-parameter fine-tuning in [Tabel](https://anonymous.4open.science/api/repo/a-8112/file/9.pdf), confirming that KIND improves performance with lower computational cost.
>**Q13:Multi-class Generation**
Multi-class generation can be achieved by setting the class gate to 1 for desired classes (see [Figure](https://anonymous.4open.science/api/repo/a-8112/file/10.pdf)).
>**Q14:Selection Criterion for Tailors**
As noted in Q10, randomly initializing tailors is simple and effective.
Future work may explore fine-tuning from similar-class tailors (e.g., Koala from Monkey in [Tabel](https://anonymous.4open.science/api/repo/a-8112/file/11.pdf)) or adaptively integrating multiple tailors via MoE.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the rebuttal. Most of my concerns have been resolved. I have updated my rating.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer abHL,
Thank you for your thoughtful evaluation, as well as for your generous score adjustment.
Your insightful feedback has been instrumental in refining our study, and we sincerely appreciate the time and effort you have dedicated to the review process.
Once again, we extend our deepest gratitude for your valuable comments!
Best regards! | null | null | null | null | null | null |
Fast Large Language Model Collaborative Decoding via Speculation | Accept (poster) | Summary: This paper introduces "Speculative Ensemble" (SE), a novel framework that accelerates Large Language Model (LLM) ensembles without sacrificing performance. While ensemble methods enhance LLMs by combining multiple models, they suffer from high computational costs. The authors build on speculative decoding—where a small model generates tokens sequentially and a larger model verifies them in parallel—with two key insights: (1) the verification distribution can be the ensemble distribution of both models, and (2) alternating each model as proposer and verifier enhances efficiency. The approach generalizes to n-model ensembles and theoretical analysis proves SE is never slower than standard ensembles. Experiments across various tasks demonstrate speed improvements of 1.11x–2.23x over standard ensemble techniques without compromising generation quality.
Claims And Evidence: The paper's claims are generally well-supported by both theoretical analysis and empirical evidence. They prove and experimentally show that the speculative ensemble improves speed without sacrificing performance, and it is not slower than an ensemble approach.
One main concern I have is that based on practical intuition, the approach does not seem to have a clear speedup over the normal ensemble. In the case of 2 models alternating, in Figure 2, at best, each model processes their tokens, and then they are verified by another model. If they are close in size, the expectation is that the parallel run of these models (normal ensemble) will be equal or better than the current proposal. This is because, in the current proposal, we have the autoregressive steps at every step (except for verification), which can run the models in parallel, and avoid extra time for verification. If the models differ in size greatly, then in half of the steps, we are doing better than the parallel ensemble, and in the other half we are not. Hence, it is not clear where the speedup is coming from.
Methods And Evaluation Criteria: The paper uses appropriate methodologies and evaluation criteria for assessing the proposed Speculative Ensemble framework. The authors evaluate their approach across diverse tasks (code generation, mathematical reasoning, multi-task understanding, and text summarization) using established benchmarks (HumanEval, GSM8K, MMLU, and CNNDM), which effectively represent a range of LLM applications. Their evaluation metrics focus on tokens generated per second and speedup ratios relative to standard ensemble methods. The experimental design includes various model pairs (Llama-Vicuna, Qwen, Llama-3, OPT), testing both two-model and three-model configurations, and comparing multiple ensemble functions (weighted ensemble and contrastive decoding). Additionally, the comprehensive ablation studies examining the impact of various parameters (λ, μ, and γ) further strengthen the evaluation by providing insights into the factors affecting performance.
Theoretical Claims: The paper provides well-structured and logical proofs for its key theoretical claims. The authors offer detailed proofs for the correctness of speculative-based ensemble (showing tokens align with the ensemble distribution), acceptance rate calculation, and the speed improvement factors.
Experimental Designs Or Analyses: The experimental design in the paper is generally sound, with a comprehensive evaluation across multiple model architectures, tasks, and ensemble functions. However, the concern mentioned above, should be addressed in some experimental results, by showcasing the profile of each run (parallel ensemble, and SD ensemble), so we can have a better understanding of how the model achieve this speedup.
Supplementary Material: Yes, I checked the validity of the proofs at a high level, and they seem fine.
Relation To Broader Scientific Literature: The proposal is an interesting approach for speeding up the ensemble methods, and can be useful in various application.
Essential References Not Discussed: Not that I am aware of.
Other Strengths And Weaknesses: mentioned above.
Other Comments Or Suggestions: NA
Questions For Authors: mentioned above.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their time and insightful comments. Below, we address each concern in detail.
**Claims And Evidence 1: compare to PE when model sizes are close**
First, we evaluate the speedup of *parallel ensemble* (PE). However, PE is even slower than the sequential ensemble. For details on the experimental setup, results, and further discussion, please refer to our response to Reviewer hXqY under 'Other Comments or Suggestions'.
Moreover, as you noted, when model sizes are comparable, SE is theoretically expected to perform similarly to or slower than PE. Nonetheless, we maintain that SE remains a promising and broadly applicable approach. Our reasoning is as follows:
1. In practice, PE is limited by its reliance on complex engineering and powerful hardware. It also requires twice the throughput and more GPU memory. Consequently, sequential ensemble is also widely used, as seen in repositories like xydaytoy/EVA, starrYYxuan/UniTE, and cmavro/PackLLM. SE can greatly speedup sequential ensemble without requiring specialized engineering or additional throughput and GPU memory, highlighting its practical potential.
2. Furthermore, if SE is equipped with the same throughput as PE (i.e., double its current throughput), it can be combined with PE to accelerate more models. For example, the 2-model ensemble in Figure 2 can be naturally extended to a 4-model ensemble. The procedural steps for this extension are detailed below, and a schematic illustration is provided in [SE with_PE](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/se_with_pe.pdf).
- Step 1: Models $\mathcal{M}_1$ and $\mathcal{M}_2$ are invoked in parallel to produce distributions $p_1^{(1)}(\cdot)$ and $p_1^{(2)}(\cdot)$. A token $x_1^{(1)}$ is sampled from $p_1^{(1)}(\cdot)$ as the proposal, and its score under $\mathcal{M}_2$, given by $p_1^{(2)}(x_1^{(1)})$, is saved.
- Step 2: Similarly, $\mathcal{M}_3$ and $\mathcal{M}_4$ are invoked in parallel to score $x_1^{(1)}$ and generate bonus distributions $p_2^{(3)}(\cdot)$ and $p_2^{(4)}(\cdot)$. A bonus token $x_2^{(3)}$ is sampled from $p_2^{(3)}(\cdot)$, and its score under $\mathcal{M}_4$, i.e., $p_2^{(4)}(x_2^{(3)})$, is saved.
- At this stage, $x_1^{(1)}$ has been scored by all 4 models and proceeds to verification. If accepted, $x_1^{(1)}$ is treated as a sample from the ensemble distribution, as illustrated in Step 3.
- Step 4: The process is repeated with $\mathcal{M}_1$ and $\mathcal{M}_2$ invoked again to score $x_2^{(3)}$ and generate new bonus distributions, mirroring the procedure in Step 2.
The algorithm retains the properties discussed in the paper, including losslessness, and it is never slower than the 4-model PE.
Note that the method described here is a preliminary version and can be further optimized. For instance, in Step 1, we can sample two tokens from both $p_1^{(1)}(\cdot)$ and $p_1^{(2)}(\cdot)$, and verify them in parallel using a tree attention to further improve the acceptance rate. We will explore this in future work to further enhance the performance of SE.
**Claims And Evidence 2: compare to PE when model sizes differ**
When the model sizes differ greatly, speedup is mainly coming from reducing the number of large model invocations.
In the optimal case, PE reduces only the computational time of the small model, while the large model remains a major time bottleneck. In contrast, SE—under setting shown in Figure 2—can halve the number of large model invocations, resulting in a substantially more effective speedup.
On the other hand, the speedup comes from allowing the smaller model focuses on sequential generation, while the larger model focuses on parallel verification. This shares a common acceleration principle with SD.
As noted on Page 5, Line 251 (left column), two hyperparameters, $\gamma_p$ and $\gamma_q$, control the proposal length for each model when acting as the proposer. When model sizes differ greatly, the larger model’s $\gamma$ is set to 1, and the smaller model is assigned a higher value (e.g., 5), as described in Section 4.1, under “Configuration of $\gamma$”. As a result, the smaller model is invoked more frequently—about 5 times as often as the larger model—rather than "half" of the total invocations. This setup ensures that the smaller model focuses on sequential proposal generation, while the larger model conducts parallel verification, echoing the acceleration strategy of vanilla SD. This is further supported by the ablation study in Figure 6(b), which demonstrates that speedup consistently increases with higher $\gamma$ values of the small model.
**Experimental Designs Or Analyses:**
We also provide a case to better illustrate how SE achieves greater speedup compared to SD; please see our response to Reviewer hXqY under "Questions for Authors".
If you have any questions or concerns, please let us know. We’re committed to addressing them.
---
Rebuttal Comment 1.1:
Comment: Thanks to the authors for their response. I have raised my score, as my concerns are mainly addressed. This paper can be a good application venue for speculative decoding.
---
Reply to Comment 1.1.1:
Comment: Thank you for the thoughtful feedback and the improved evaluation. We’re glad that our responses addressed your concerns and that you see the paper’s potential as a good application venue for speculative decoding. We will integrate the rebuttal points into the revision to further improve the paper. | Summary: The authors extend speculative decoding to ensemble models and demonstrate, through both theoretical analysis and empirical results, that their approach outperforms standard ensemble baselines.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: The theoretical analysis largely follows the original speculative decoding framework, but appears to be correct.
Experimental Designs Or Analyses: 1. Do you test larger models, larger than 7B?
2. Could you design experiments to compare with more baselines/related works? Only comparing with pure ensemble models and the original speculative decoding seems insufficient to fully evaluate the contribution of the proposed method.
Supplementary Material: I checked the proofs and additional experiments.
Relation To Broader Scientific Literature: Speculative decoding is important for efficient AI.
Essential References Not Discussed: Not that I'm aware of.
Other Strengths And Weaknesses: Strengths:
1. The proposed method shows improvements over standard ensemble models, demonstrating its practical value within that setting.
Weaknesses:
1. The method appears to be a relatively minor adaptation of standard speculative decoding applied specifically to ensemble models, which raises concerns about its general applicability beyond this narrow use case.
2. The theoretical analysis closely follows prior speculative decoding work and does not introduce significantly novel insights.
3. It is unclear whether the authors have compared their approach against strong non-ensemble baselines. A comparison in terms of speedup and accuracy trade-offs with single-model speculative decoding would help contextualize the contribution.
4. The paper includes limited baseline comparisons, making it difficult to assess the overall effectiveness and competitiveness of the proposed method.
Other Comments Or Suggestions: No minor issues.
Questions For Authors: 1. Could you compare the speedup and accuracy trade-offs with single-model speculative decoding, not just with ensemble models?
2. Have you tested on larger models? How does the model size affect the results?
3. How does the method compare with batch speculative decoding methods such as Medusa [1]?
4. Could you design experiments to compare with more baselines/related works? Only comparing with pure ensemble models and the original speculative decoding seems insufficient to fully evaluate the contribution of the proposed method.
[1] Cai, Tianle, et al. "Medusa: Simple llm inference acceleration framework with multiple decoding heads." arXiv preprint arXiv:2401.10774 (2024).
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for their time and insightful comments. Below, we address each concern in detail.
For clarity and brevity, we use the following abbreviations: Experimental Designs Or Analyses (EDOA), Weaknesses (W), and Questions (Q).
**W1: Speculative Ensemble (SE) offers two non-trivial improvements over vanilla SD.**
Compared to simply adapting vanilla SD to ensemble scenarios, SE offers two non-trivial improvements:
1. Compared to vanilla SD, where one model consistently serves as the proposer and the other as the verifier, we introduce an alternating proposal framework (APF) in Section 3.3, as shown in Figure 2. This method switches the roles of proposer and verifier during decoding, and is specifically designed to enhance efficiency in ensemble settings. We also validate its effectiveness through ablation experiments shown in [Ablation of APF](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/ablation_of_apf.md). For a case-specific explanation, please refer to our response to reviewer hXqY under 'Questions for Authors'.
3. Unlike the vanilla SD, which employs two models, the proposed SE extends to an n-model scenario to accelerate the n-model ensemble in Section 3.4, as shown in Figure 3 and Figure 7.
Moreover, Reviewer hXqY described our method as “clever, novel, and well-validated,” while Reviewer 3eWy referred to it as a “novel framework,” both highlighting the non-trivial improvements offered by our approach.
**W1: concerns about general applicability**
Our proposed SE not only accelerates traditional weighted ensemble (WE) methods (Eq 4), but also accelerates ensembles of any form, size, or number of LLMs at the probability or logits level. This includes techniques such as contrastive decoding (CD) [1] (Eq 5) and decoding-time realignment [2], demonstrating its broad applicability. As Reviewer 3eWy noted, SE “can be useful in various application,” further supporting this point.
**W2: concerns about theoretical novel insights**
While our theoretical analysis of correctness (i.e., losslessness) and speedup follows original SD paper, we introduce two novel theoretical insights tailored to the ensemble scenario:
1. As discussed on page 4, line 205 (left column), in vanilla SD, estimating the expected speedup requires extensive experiments to estimate the acceptance rate $\alpha$. However, in WE setting, the parameter $\lambda$ (Eq 4) naturally serves as a lower bound for $\alpha$. This allows us to estimate the speedup in advance and choose a suitable proposal model, such as those described in Corollary 3.5.
2. Vanilla SD does not guarantee acceleration; in fact, it may result in slower speed when $\alpha$ is small. In contrast, SE is theoretically proven to be no slower than the standard ensemble, even in the worst case, as established in Corollary 3.7.
**Q1, 3, 4 & W3, 4: compare with more baselines**
Thank you for your valuable suggestions. To better demonstrate SE, we conducted experiments comparing SE with three non-ensemble baselines: Large Model, vanilla SD, and Medusa. The results are shown in [Non-ensemble](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/non_ensemble.md). Note that for Medusa, we only reported the results for Vicuna, because it only provides the pretrained draft model for Vicuna. For Qwen-3B, we did not report results for vanilla SD, because there is no suitable draft model for it.
Additionally, it is important to note that SE, as an acceleration algorithm, is a line of research parallel to SD. It does not focus on finding a quality-speed trade-off. Instead, SE focus on accelerates inference while preserving the performance gains provided by ensemble.
**EDOA1 & Q2: results for models larger than 7B and the impact of model size**
As described in Section 4.1, "Model Pair Configuration" and in Table 1, we evaluated the CD setting using the model pair (OPT-13B, OPT-125m). The corresponding results are presented in Table 4.
In addition, we also tested a larger model pair (Llama-2-13B, Vicuna-13B) under the WE setting. The results are shown in [Larger Model](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/larger_model.md).
Together with the results in Tables 2 and 3, we observe that SE achieves greater speedup as model size increases in both the WE and CD scenarios, with a more pronounced effect in CD. In WE, this trend may be due to improved model performance with larger sizes, which increases similarity between models and leads to a higher acceptance rate. In the CD scenario, the growing speedup may stem from the increasing cost of invoking the larger model.
If you have any further questions or concerns, please feel free to let us know. We are committed to addressing any concerns to the best of our ability.
[1] Contrastive Decoding: Open-ended Text Generation as Optimization
[2] Decoding-time Realignment of Language Models
---
Rebuttal Comment 1.1:
Comment: Thank you for the rebuttal. Based on the non-ensemble comparisons, where the proposed method is significantly slower than standard speculative decoding (SD), I remain unconvinced that applying speculative decoding to weighted ensembles offers broadly applicable benefits. Therefore, I am inclined to maintain my original score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response. We think that several key points in our paper still require clarification.
**1. Standard SD and SE achieve different types of acceleration and are not comparable**
Take the Llama-Vicuna model pair as an example. Standard SD accelerates a **single 7B model**, whereas the WE-SE results are based on an ensemble of **two 7B models**. Since a single model naturally runs faster than an ensemble, directly comparing their speeds is inappropriate.
A more appropriate comparison is between WE-SE and WE-SD—the latter applies SD directly to the ensemble, as described in Section 4.1, *“Ensemble functions and methods.”* As shown in Table 2, WE-SE achieves significantly greater speed than WE-SD.
**2. The benefits of applying SD or SE to weighted ensembles**
As shown in our [Raw Speed](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/raw_speed.md) results, if someone wants to ensemble Llama and Vicuna, the standard ensemble can only achieve a speed of only 22.617 tokens/sec. In contrast, applying SD (WE-SD) increases the speed to 28.723 tokens/sec, and applying SE further boosts it to 35.734 tokens/sec, resulting in a substantial efficiency improvement.
Additionally, it is important to note that **single-model SD approaches can not accelerate the ensemble**. | Summary: ## Update after Rebuttal
My concern regarding the insufficient analysis of the quality–speedup trade-off was addressed by the authors’ rebuttal, therefore I have reflected this by increasing my score from 2 to 3, i.e., leaning towards acceptance.
However, the results of comparing with non-ensemble baselines suggest that the proposed method is ~$2\times$
slower than standard speculative decoding (as also noted by Reviewer m8L7). This prevents me from giving a higher rating.
IMHO, this actually raises concerns about the necessity of using the ensemble approach --- when comparable or even better performance might be achievable by pairing a small and a large model (e.g., 1B–14B in standard speculative decoding), using two models of similar size as in the ensemble setup (e.g., 7B–7B) seems unnecessary since the non-ensemble methods could potentially lead to both faster generation speed and better generation quality.
On a related note, this ICLR 2025 paper (SpecCascade [1]) appears to be a closely relevant work, which is able to provide better cost-quality trade-offs than their sequential cascade and speculative decoding counterparts. **Given the similarity between Speculative Ensemble and SpecCascade, it is suggested that the authors discuss this work and better position the unique contribution of the submission.**
[1]. Faster Cascades via Speculative Decoding, ICLR 2025.
## Original Summary
This paper introduces Speculative Ensemble (SE), a method designed to accelerate large language model (LLM) ensembles by leveraging speculative decoding principles. Instead of computing ensemble predictions independently for each model, SE employs a verification scheme where models alternate as proposers and verifiers. The paper claims that this design maintains ensemble quality compared to standard ensemble methods while achieving faster decoding speeds. Theoretical analysis demonstrates that the proposed SE is guaranteed to be no slower than a standard ensemble under certain assumptions. Empirical results on benchmarks such as HumanEval, GSM8K, MMLU, and CNNDM show speedups ranging from 1.11x to 2.23x over standard ensembles. However, no comparison of generation quality is provided.
Claims And Evidence: - The claim that Speculative Ensemble (SE) maintains performance compared to standard ensembles lacks empirical validation. In Section 4, the experiments primarily focus on speedup comparisons, while no quality metrics (e.g., accuracy) are provided to confirm that speculative ensembling does not degrade generation performance. As a result, it remains unclear whether SE preserves the benefits of ensembling.
Methods And Evaluation Criteria: - Lack of generation quality evaluations. While the speedup metric (tokens per second) is reasonable, the absence of generation quality evaluations is a significant concern. As stated in Corollary 3.5, there exists a hyperparameter $\lambda$ such that the proposed Speculative Ensemble (SE) is guaranteed to be at least as fast as a standard ensemble. However, the choice of $\lambda$ inherently impacts ensemble quality. Although certain values of $\lambda$ may lead to speedups, they could also result in performance degradation, potentially making SE less effective than non-ensemble methods or standard ensemble methods. Without empirical evidence demonstrating that SE improves generation quality, the practical utility of the method remains uncertain.
- Insufficient baseline comparisons. The authors do not compare SE against non-ensemble baselines to demonstrate its effectiveness in terms of generation speedup and quality. A basic evaluation setup should include the following typical baselines: 1) single-model baselines: using only the large or smaller model alone for token generation. 2) standard speculative decoding: employing a fixed small model as the drafter and a large model as the verifier for token generation.
Without such comparisons, it is difficult to assess whether SE provides meaningful improvements over simpler or more established approaches.
Theoretical Claims: The mathematical proofs seem correct, but they do not address whether SE actually improves generation quality.
Experimental Designs Or Analyses: - The experiments demonstrate speedup but fail to evaluate generation quality.
- The quality-speed tradeoff study in Appendix C.1 is insufficient. No ablations are provided to separate the impact of speculative decoding vs. ensemble benefits.
- The paper does not compare SE against simpler baselines, such as using the large model alone or using a standard speculative decoding setup with one small drafter and one large verifier (w/o alternating the drafter and verifier).
Supplementary Material: N/A
Relation To Broader Scientific Literature: The paper borrows principles from speculative decoding and applies them to LLM ensembles.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Other Strengths
- An interesting attempt to extend speculative decoding to ensemble settings
Other Weaknesses
- Missing comparisons with simpler baselines
- No empirical validation of quality preservation—only speedup is measured
- Alternating proposer/verifier is not clearly justified—it may degrade efficiency and quality
Other Comments Or Suggestions: N/A
Questions For Authors: 1. How does Speculative Ensemble (SE) impact generation quality compared to baseline methods?
2. The ensemble setup seems less practical. While pairing a smaller model with a large model is common in speculative decoding, ensembling is typically used with comparable models to achieve further performance gains. In what scenarios would it be necessary to ensemble a large model with a much smaller model? How does SE compare to simply using a single large model? Is ensembling actually necessary for performance gains in the setting described in this paper?
3. Can the authors justify why alternating between proposer and verifier roles improves efficiency, rather than using the large model exclusively for verification? This finding appears to depend on the specific choice of drafter and verifier models. Would the same efficiency gains hold if the drafter and verifier models were of comparable sizes?
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their time and insightful comments. Below, we address each concern in detail.
For brevity, we use the following abbreviations: Claims and Evidence (CAE), Methods and Evaluation Criteria (MAEC), Theoretical Claims (TC), Experimental Designs or Analyses (EDOA), Weaknesses (W), and Questions for Authors (Q).
**CAE & MAEC1 & TC & EDOA1 & W2 & Q1: concerns about generation quality**
We apologize for the lack of clarity regarding generation quality. In the SD domain, performance is theoretically well-established, so researchers typically focus on comparing speed rather than performance [1] [2] [3]. Our approach follows this standard practice.
From both theoretical and experimental perspectives, we confirm that SE consistently maintains ensemble quality.
Theoretically, as shown in Appendix A.1, we proved that the generated tokens precisely follow the ensemble distribution—that is, they can be regarded as samples from this distribution. Reviewers hXqY, A7ww, and 3eWy also endorsed the correctness of our proof.
To further validate this, we conducted additional experiments. As shown in [Generation Quality](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/generation_quality.md), when T=0, the performance is exactly the same (as proved in Section 3.2 of [4]), while when T=1, due to randomness, the performance shows slight differences but remain largely consistent. For the weighted ensemble (WE), we report only T=1 case, as T=0 is uncommon in WE setting, as discussed in Section 4.1 "Ensemble functions and methods".
**MAEC1 : concern about Corollary 3.5**
Corollary 3.5 states that for any given $\lambda$, there exists a $\gamma$ that guarantees an ensemble speedup. Notably, $\lambda$ is not a hyperparameter of the SE algorithm; instead, the proposal length $\gamma$ is. As an acceleration method, SE aims to speed up the ensemble under a given $\lambda$. The selection of $\lambda$ follows the same procedure as in standard ensembles—that is, it is set to the value that yields the best performance. For example, [5], [6], and [7] respectively set $\lambda$ based on the trade-off between model purification and standard performance, the performance on a development set, and the perplexity.
In addition to accelerating common weighted ensembles (Equation (4)), the proposed SE can also speed up any form of probability- or logits-level ensembles (Equation (3)). In this more general setting, Corollary 3.7 provides a theoretical guarantee of SE's acceleration.
**MAEC2 & EDOA3 & W1: compare with non-ensemble baselines**
Regarding this, please refer to our response to Reviewer m8L7 under "Q1, 3, 4 & W3, 4".
**Q2: the practicality of ensemble small and large models**
Regarding this question, please refer to our response to Reviewer A7ww under "MAEC1".
**EDOA2: concerns about ablations**
First, the quality-speed tradeoff in Appendix C.1 is not a central focus of the paper, please refer to our response to Reviewer A7ww under "MAEC2" for a more detailed explanation.
Second, we did not separate the impact of speculative decoding and ensemble benefits because SE is designed specifically for ensemble scenarios, rather than treating ensemble as a separate component. While it is well known that ensemble can enhance LLM performance, it typically incurs slow inference. SE aims to accelerate inference while preserving these performance gains.
**W3 & Q3: concerns about alternate proposal**
First, please refer to our response to Reviewer hXqY under "Questions For Authors" for an example illustrating the impact of using the alternate proposal framework (APF). As shown, APF enables the generation of an additional bonus token within the same number of model invocation, thereby enhancing efficiency.
Second, our ablation study confirms the effectiveness of APF. The results are shown in [Ablation of APF](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/ablation_of_apf.md).
Third, as detailed in Section 4.1, "Ensemble Functions and Methods" and Table 1, we evaluated 4 groups of comparable model configurations (e.g., Llama-2-7B + Vicuna-7B). The results in Table 2 show that APF can still enhance efficiency if the drafter and verifier models are of comparable sizes.
If you have any further questions or concerns, please feel free to let us know. We are committed to addressing any concerns to the best of our ability.
[1] Fast Inference from Transformers via Speculative Decoding
[2] EAGLE: Speculative Sampling Requires Rethinking Feature Uncertainty
[3] GliDe with a CaPE: A Low-Hassle Method to Accelerate Speculative Decoding
[4] Speculative Decoding: Exploiting Speculative Execution for Accelerating Seq2seq Generation
[5] Purifying Large Language Models by Ensembling a Small Language Model
[6] Ensemble Learning for Heterogeneous Large Language Models with Deep Parallel Collaboration.
[7] Relative representations enable zero-shot latent space communication
---
Rebuttal Comment 1.1:
Comment: I thank the authors for answering my questions and providing additional experimental results.
Regarding the concern about generation quality, I was referring to the fact that the hyperparameters $\lambda$ (for WE) and $\mu$ (for CD) can affect the effectiveness of the methods.
As shown in Figure 8, to achieve higher speedups in WE-SE and CD-SE, $\lambda$ and $\mu$ need to be carefully chosen. **However, the optimal configuration of $\lambda$ and $\mu$ for WE-SE and CD-SE might not be the same as that for WE and CD.** I understand that speculative decoding maintains output consistency, but for ensemble methods, the selection of $\lambda$ and $\mu$ that optimizes ensemble performance may not lead to the best speedup for WE-SE and CD-SE. So there could be a trade-off.
For example, under the current setting of $\lambda=0.5$ and $\mu=0.1$, WE-SE and CD-SE can maintain the same generation quality as WE and CD (since they share the same hyperparameters) while achieving faster generation. However, the optimal performance of WE and CD might occur under a different hyperparameter choice (say, $\lambda=0.9$ and $\mu=0.3$), under which WE-SE and CD-SE might not achieve meaningful speedups.
Therefore, I think my question is: **when WE and CD use their own optimal $\lambda$ and $\mu$ values (which may differ from the optimal configuration for WE-SE and CD-SE since they need to balance the generation quality and speedup), what is the resulting generation quality of WE-SE and CD-SE compared to WE and CD?**
---
Reply to Comment 1.1.1:
Comment: We apologize for the earlier misunderstanding regarding your concern about generation quality and appreciate your thoughtful follow-up. We remain committed to addressing your remaining concerns with clarity and thoroughness.
**1. The choice of $\lambda$ and $\mu$ in SE**
In the proposed SE, the parameters $\lambda$ and $\mu$ are not chosen to balance ensemble performance and speedup. Instead, we recommend the following strategy for using SE:
1. First, identify the optimal value of $\lambda$ or $\mu$ in the standard ensemble—that is, the value that yields the greatest performance improvement.
2. Then, using this optimal $\lambda$ or $\mu$, apply SE to further accelerate the ensemble while preserving this optimal performance gain.
Under this selection strategy, high generation quality is well ensured. However, as you correctly noted, SE may not achieve the optimal acceleration. Nonetheless, our ablation study demonstrates that SE still provides a substantial acceleration.
In WE setting, as discussed in Section 4.3 "Speedup ratio for different weight $\lambda$ in WE" and illustrated in Figure 4, our experiments demonstrate that WE-SE consistently achieves a high speedup of at least 1.5x across all tested $\lambda$ values from 0.1 to 0.9. This indicates that in practical scenarios, regardless of what the optimal configuration of $\lambda$ is, WE-SE can achieve substantial acceleration.
In CD setting, as discussed in Section 4.3 "Speedup ratio for different weight values of $\mu$ in CD" and illustrated in Figure 5, our experiments show that although the speedup of CD-SE gradually declines as increasing $\mu$ increases, CD-SE still offers a substantial acceleration. In addition, we report the performance of CD across a range of $\mu$ values in [CD across Different mu](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/cd_across_different_mu.md). The results indicate that optimal performance is generally achieved at smaller $\mu$ values such as 0.1 or 0.2, which also deliver notable speedups.
**2. The choice of $\lambda$ and $\mu$ in the main experimental setup**
For our main results, we set $\lambda = 0.5$ and $\mu = 0.1$. This choice was guided not by a focus on speed, but by prior research and our empirical observations, aligning with values commonly used in practice.
In WE setting, using average weights—such as $\lambda = 0.5$ for a two-model ensemble or $\lambda_i = 1/3$ for a three-model ensemble—is the most commonly adopted approach [1] [2] [3]. Huang et al. also noted in Section 3.5 of [2] that average weighting is "the most common practice".
In CD setting, the results presented in [CD across Different mu](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/cd_across_different_mu.md) show that CD consistently improves performance only when $\mu = 0.1$. Therefore, we adopt $\mu = 0.1$ in our main experiments to maintain consistency and facilitate comparison across results.
**3. Clarification regarding Figure 8**
As outlined in Section 4.1, "Ensemble Functions and Methods", and summarized in Table 1, our experiments mainly focus on two settings: *WE with models of comparable sizes* and *CD with models of different sizes*. Figure 8, however, presents results for *WE with models of different sizes*—a setting we view as a potential application of SE, rather than a central focus of this work.
Notably, in the WE setting, as shown in Figure 4 and previously discussed, WE-SE achieves robust acceleration across all values of $\lambda$ without the need to be “carefully chosen”.
[1] Breaking the Ceiling of the LLM Community by Treating Token Generation as a Classification for Ensembling
[2] Ensemble Learning for Heterogeneous Large Language Models with Deep Parallel Collaboration
[3] Determine-Then-Ensemble: Necessity of Top-k Union for Large Language Model Ensembling | Summary: This paper proposes Speculative Ensemble, accelerating ensemble speed without sacrificing the ensemble quality, inspired by speculative decoding. They theoretically prove the speed improvement over standard ensemble approaches. Experimental results also support their arguments and better ensemble efficiency.
Claims And Evidence: While vanilla ensemble approaches require sequential calls of all models, the proposed methods smartly leverage Speculative decoding to make it more efficient. Theoretical guarantee for speedup is also supporting the claim very well.
Methods And Evaluation Criteria: - If the proposal and verifier differ a lot (i.e., small $c$), setting $\lambda$ larger than $\frac{c}{1+c}$ will naturally increase the acceptance rate and speed obviously. However, we know that there's a trade-off where performance might degrade as it converges towards the proposal model's performance. Using an ensemble, there could be an optimal $\lambda$ for peak performance, but this method doesn't seem to offer a way to find that optimal value. While ensemble intuitively speeds things up, uniform weights like 0.5 or 0.3 are likely near-optimal only when model sizes are similar. Combining small and large models might introduce inefficiency in finding the right trade-off.
- Regarding this, Figure 8 suggests that with differing model sizes, there isn't a clear optimal $\lambda$, and ensembling the proposal distributions doesn't seem to help performance. It's unclear if ensembling actually improved overall performance through this graph. In such settings (llama-3, -2, opt), a comparison of the accuracy-speedup trade-off with vanilla SD would be useful. Can you show a performance comparison between them given the same throughput?
- Also, if ensembling small model distributions is less effective, I don't see the benefits for verifying bonus tokens. Of course, it makes sense if it helps performance with similar sized models, and I think that efficient refinement of bonus tokens could be possible during autoregressive generation after the swap.
Theoretical Claims: I’ve reviewed the theoretical claims well. One question I have is regarding Corollary 3.5, which states that if the proposer and verifier are swapped (alternate proposal framework), there is acceleration when $\lambda < \frac{c}{1+c}$. Have these things been reflected upon or considered? It seems like the same $\lambda$ is used even when switching.
Experimental Designs Or Analyses: The validation is too focused on speed, and there's no performance trade-off from the ensemble. While it's clear that it's faster than existing ensembles, I'd like to see the performance gain from the ensemble as well. A clearer comparison of speed and performance with existing SD-based methodologies that used model ensembles would be helpful.
Supplementary Material: I checked the supplementary material.
Relation To Broader Scientific Literature: I found the concept of using SD for model ensembling interesting. However, I'm not sure how much gain there is in terms of speed and performance compared to existing methodologies in the SD literature that used combinations of two distributions (small-large).
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: I’d be happy to discuss with the authors.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their time and insightful comments. Below, we address each concern in detail.
For clarity and brevity, we use the following abbreviations: Methods and Evaluation Criteria (MAEC), Theoretical Claims (TC), Experimental Designs or Analyses (EDOA).
**MAEC1: contrastive decoding is the ensemble function in our setup when model sizes differ**
As discussed in Section 4.1 "Ensemble Functions and Methods" and summarized in Table 1, for model pairs like Llama-3, -2, and OPT, where the proposer and verifier differ a lot, we applied **contrastive decoding (CD)** [1] rather than the traditional weighted ensemble (WE).
CD enhances token generation quality by subtracting the logits of a smaller model from those of a larger one, as defined in Equation (5). When combined with CD, LLMs generally achieve improved performance. To support this, we present results using Llama-3 and -2 with CD, and compare them to the large model baseline, as detailed in [CD](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/cd.md).
Therefore, when model sizes differ, our method is not intended to trade performance for speed. Instead, our focus is, when an ensemble method (e.g., CD) improves LLM performance, SE can further accelerate the ensemble while preserving these gains.
Additionally, it is important to point out that, as shown in Section 4.1 ("Ensemble Functions and Methods") and Table 1, we also evaluated the speedup of SE under the WE setting when model sizes are similar. The results are presented in Table 2.
**MAEC2: about weighted ensemble when model sizes differ in Figure 8**
Although this paper primarily focuses on CD when model sizes differ, we also introduce WE with different model sizes as an exploratory approach to the quality-speed tradeoff. This discussion appears on page 4, line 203 (right column), with the corresponding results shown in Figure 8. However, this is not a central focus of the paper; rather, we present it as a potential strategy for achieving faster acceleration in vanilla SD—specifically, by applying WE with the proposal model and using SE.
In this context, $\lambda$ serves as a hyperparameter that governs the quality-speed tradeoff. One possible selection strategy is to choose the largest $\lambda$ such that the ensemble performance exceeds a predefined threshold. As shown in Figure 8, a larger $\lambda$ indicates greater acceleration. Therefore, this selection strategy ensures that the highest speed is achieved while meeting the performance requirements.
**MAEC3: concerns about verifying bonus tokens from small model**
First, as previously noted, when model sizes differ, our primary focus is on CD. This ensemble approach can outperform a single large model. Therefore, verifying bonus tokens is meaningful.
In the context of WE with different model sizes, as you noted, verifying bonus tokens from the large model typically leads to reduced performance. Therefore, using the bonus tokens directly without verification is a more suitable approach. We appreciate your constructive feedback and will reflect it in the revised version. That said, our design prioritizes interpretability—specifically, ensuring that the distribution of generated tokens remains controllable and consistent. Consequently, in some cases, it remains beneficial to verify bonus tokens produced by the large model. For instance, as mentioned on page 5, line 231 (left column), some studies suggest that appropriately ensembling a smaller model can enhance safety.
**TC: about Corollary 3.5**
The term "swap" in Corollary 3.5 does not refer to the dynamic role alternation between proposer and verifier in the alternate proposal framework.
Corollary 3.5 is specifically formulated for the Speculative-based Ensemble, which includes only the methods introduced in Section 3.2 and excludes the alternate proposal framework. It states that when the proposer and verifier are fixed, choosing an appropriate proposer model before inference begins can ensure acceleration. For example, when ensembling $\mathcal{M}_p$ and $\mathcal{M}_q$, if using $\mathcal{M}_p$ as the proposer does not guarantee acceleration, then $\mathcal{M}_q$ must. The "swap" referenced in Corollary 3.5 refers to this initial selection at the start of inference and does not occur dynamically during the inference process.
Additionally, Corollary 3.7 guarantees the acceleration of SE under the alternate proposal framework. This corollary provides a more general result that ensures acceleration for any form of ensemble, not just WE.
**EDOA & MAEC2: compare to single model SD**
Regarding this, please refer to our response to Reviewer m8L7 under "Q1, 3, 4 & W3, 4".
If you have any further questions or concerns, please feel free to let us know. We are committed to addressing any concerns to the best of our ability.
[1] Contrastive Decoding: Open-ended Text Generation as Optimization
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Rebuttal Comment 1.1:
Comment: Thanks for the detailed explanation to address my questions. I missed the parts that CD is used when the model sizes differ.
All my concerns are resolved, and I believe this paper is above the acceptance bar.
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Reply to Comment 1.1.1:
Comment: Thank you for the thoughtful and constructive feedback. We're glad that our responses addressed your concerns and appreciate your positive assessment. We will incorporate the rebuttal points into the revision to further improve the paper. If the clarifications merit a score revision, we would be grateful for your consideration. | Summary: This paper proposes "Speculative Ensemble", a method for speeding up auto-regressive generation from LLM ensembles using ideas from speculative decoding. For example, in the case of a two model ensemble, one can treat one of the models as the draft model, generate tokens with that model, and then process those tokens with the other model, with the important twist that during the verification algorithm the ensemble distribution is used as the target distribution (instead of directly using the "verifier's" distribution). This method can be extended to ensembles with > 2 models. Additionally, this method can be used to explore speed-quality trade-offs when using a weak model as the draft model and a strong model as the target model---as you assign larger weight to the draft model in the ensemble distribution, the acceptance rate and speed goes up, but the quality of the generation goes down.
Theoretically, the paper proves that speculative ensemble is always at least as fast as the naive ensembling approach of running each model independently.
Empirically, the paper shows across a variety of tasks that the proposed method attains 1.11x-2.23x speedup over the naive ensembling approach.
Claims And Evidence: Yes, the claim are support by clear and convincing evidence across numerous model pairs and tasks.
Methods And Evaluation Criteria: Yes, the proposed methods and evaluation criteria make sense. I found the "alternate proposal framework", as well as the extension of this method to N models, clever. The theoretical analysis is interesting and illuminates the speedups that should be expected from this method.
It would have been useful to report the "raw speeds" attained by the proposed method, to compare with SOTA in the literature.
Theoretical Claims: I (relatively quickly) checked the proofs of the claims in the main paper, and did not find any issues. The results make sense to me.
Experimental Designs Or Analyses: Yes, I did not see any issues.
Supplementary Material: I looked at Appendix C.1, which shows speed-quality trade-offs when ensembling weak and strong models.
Relation To Broader Scientific Literature: To the best of my knowledge, this paper is the first to show how to use speculative decoding to sample from a distribution which is computed by combining two or more other model distributions. The method relates to the broader literature on speculative decoding and on how to speed up autoregressive generation from LLMs.
Essential References Not Discussed: I am not aware of any key references that weren't discussed.
Other Strengths And Weaknesses: The method is clever, novel, and well-validated. I see no glaring weaknesses.
Other Comments Or Suggestions: It could be worth comparing with the very strong baseline of running the different models in the ensemble on difference devices, simply as a reference point (each model processes the last generated token in parallel, then the ensemble distribution is computed, and then a token is sampled from that distribution).
Questions For Authors: In Tables 2 and 3, what exactly is the SD method? Does it simply throw away the bonus token?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for the time and effort spent reviewing our submission and greatly appreciate your insightful comments and constructive suggestions. Below, we have done our best to address each of your concerns in detail.
**Methods And Evaluation Criteria: report the "raw speeds"**
We sincerely thank you for your insightful suggestions. To better showcase SE's performance, we have reported raw generation speeds, as presented in [Raw Speed](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/raw_speed.md).
As you correctly noted, SE is the first method proposed to accelerate any form of LLM ensemble. We have extended SD baselines to the ensemble scenario where possible and included them in our comparisons. Other SOTA methods in SD, such as EAGLE [1] and Medusa [2], might also be adapted to ensemble scenario, but doing so would require specific modifications, which are beyond the scope of this work.
**Other Comments Or Suggestions: compare with the very strong baseline**
Thank you for your valuable suggestion. For clarity, we refer to the strong baseline you identified as the *parallel ensemble* (PE).
First, we use the popular LLM ensemble repository yaoching0/GaC to test the speed of PE and implement a corresponding sequential ensemble to compute speedup. However, as shown in [Parallel Ensemble](https://anonymous.4open.science/r/SE-Rebuttal-Supplement-ICML25-667C/pe.md), PE is even slower than the sequential ensemble.
The inefficiency likely stems from overly frequent communication. In particular, during the generation of each token, PE requires communication between the main node and two GPUs. Because the time to generate a single token is very short (especially when kv cache is enabled) the communication overhead becomes significant, introducing noticeable latency. In contrast, standard sequence-level parallelism avoids this issue, as the time to generate an entire sequence is much longer than the communication time, rendering the overhead negligible. These findings further underscore the importance of SE. Note that the speed reported in the original GaC repository was measured with kvcache disabled. In contrast, our tests were conducted with the kvcache enabled, as it is commonly used in current LLM inference. Therefore, our setup provides a more realistic evaluation.
Additionally, the speedup achieved by PE is closely tied to its implementation and the underlying hardware. With improved engineering and more powerful hardware, PE could potentially attain greater speedup. Nonetheless, we maintain that SE remains a promising approach. For a detailed explanation, please see our response to Reviewer 3eWy under "Claims and Evidence 1".
**Questions For Authors: the SD method in Tables 2 and 3**
We apologize for the earlier lack of clarity.
We use an example to clarify this SD process: In each cycle, suppose the proposal model $\mathcal{M}_q$ sequentially generates 5 tokens, which are then verified in parallel by the target model $\mathcal{M}_p$, resulting in 6 distributions, where the first 5 ones correspond to the verified distributions of 5 proposal tokens, while the 6-th is the bonus distribution. Since the 6-th bonus distribution lacks a corresponding distribution from $\mathcal{M}_q$ to compute the ensemble distribution, we cannot directly sample the bonus token from the ensemble distribution. To resolve this, we invoke $\mathcal{M}_q$ again to produce the 6-th distribution. Finally, we apply the standard accept-reject criterion in SD.
Compared to this SD baseline, SE addresses this by treating the 6-th token as a proposal from $\mathcal{M}_p$ and verifies it using $\mathcal{M}_q$. This verification not only obtains the 6-th distribution from $\mathcal{M}_q$, but also generates an additional bonus token from $\mathcal{M}_q$. In the next cycle, only 4 invocations to $\mathcal{M}_q$ are needed to form the proposal, thus reducing one invocation of $\mathcal{M}_q$ compared to the SD in Tables 2 and 3.
As described above, the SD in Tables 2 and 3 does not throw away the bonus token; instead, it utilizes the token in the same manner as the standard SD. However, as previously discussed, SE utilizes bonus tokens more efficiently. With the same number of model invocations per cycle, it can generate one additional bonus token, resulting in greater acceleration.
If you have any further questions or concerns, please feel free to let us know. We are committed to addressing any concerns to the best of our ability.
[1] EAGLE-3: Scaling up Inference Acceleration of Large Language Models via Training-Time Test
[2] Medusa: Simple LLM Inference Acceleration Framework with Multiple Decoding Heads | null | null | null | null |
STD-FD: Spatio-Temporal Distribution Fitting Deviation for AIGC Forgery Identification | Accept (poster) | Summary: In this paper, the authors propose a deepfake detection method based on “temporal distribution fitting deviations.” Specifically, they argue that existing reconstruction-based approaches treat the diffusion model as a black box, which limits their generalizability. In contrast, the authors decouple the sampling process and detect forgery features by predicting temporal inconsistencies across different time steps.
Claims And Evidence: The claims in the methodology section are clear. However, the paper does not thoroughly discuss how the proposed method specifically addresses its motivation—for instance, how it effectively eliminates the strong coupling between the reconstruction model and the detection method. Additionally, it remains unclear whether the DFactor exists across all models and whether it follows the same distribution in different models.
Methods And Evaluation Criteria: The evaluation metrics are feasible.
Theoretical Claims: The proposed pipeline, ie, DFactor set construction, DFactor selection, and forgery detection, is relatively clear. However, the reviewer is confused on the Spatial Information Capture. Specifically, why does the use of superpixels lead to improved performance in diffusion models? Is there any theoretical justification for this claim? The paper does not seem to provide a rigorous explanation, leaving this aspect unconvincing.
Experimental Designs Or Analyses: The experimental setting is sound.
Supplementary Material: The reviewers did not thoroughly examine the supplementary materials.
Relation To Broader Scientific Literature: The proposed method should primarily be considered within the scope of Deepfake detection, especially for detecting forgeries generated by diffusion models. Whether it possesses strong detection capabilities and generalization ability for other types of forgeries remains an open question and requires further discussion.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: In addition to the aforementioned unclear descriptions, there are additional concerns:
1. Regarding the “Mismatch Between Pre-trained Model and Identification Target”, while the authors demonstrate strong performance of the proposed method under this condition, it remains unclear why the method is able to mitigate this issue to such a significant extent. A more detailed explanation is needed to support this claim.
2. What specific diffusion model is used in STD-FD? Is this model interchangeable? If so, how does the detection performance change when a different diffusion model is used?
Other Comments Or Suggestions: N/A
Questions For Authors: If the authors can address the concerns, the reviewer would consider increasing the rating.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for recognizing our work. Below are our responses to your questions (Q).
**Q1: Methodological Coupling & DFactor Universality**
Sorry for the misunderstanding. Reconstruction-based approaches rely on the magnitude of reconstruction error to distinguish real from fake images. When the reconstruction model encounters data from an unfamiliar domain, its robustness deteriorates. Our method instead uses a diffusion model to map images into a latent space, from which we **extract their temporal variations**.
>To illustrate, consider a simplified scenario in which 5 and 80 represent pixel values from two distinct domains. Reconstruction-based methods attempt to reconstruct them (e.g., 5 → 4.9 and 80 → 70), leading to large errors when dealing with domain shifts (e.g., transitioning from cat to human, or from a diffusion-generated fake to a GAN-generated fake). In contrast, our approach **tracks the feature variation over time**, such as:
1 → 2 → 3 → 4 → 4.9 and 50 → 55 → 60 → 65 → 70. Although the numerical values differ greatly, both sequences share a **similar variation trend** (akin to a slope in mathematics or acceleration in physics). Based on this observation, we design a spatio-temporal distribution modeling framework centered on DFactor, thereby decoupling from semantic content.
To clarify this principle, we visualized the average temporal changes of 256 pixels for cross-domain forgery data projected into latent space. The results show (Following the guidelines of this rebuttal, visualizations can be seen on anonymous website https://anonymous.4open.science/r/STDFD_re/README.md , if interested) :
- Significant Differences between Real and Fake Data: Real images exhibit irregular, larger-scale changes due to the absence of fixed generative constraints, whereas forgeries conform to specific generative paradigms (GAN/diffusion/autoregressive) and have smaller, more uniform variation patterns.
- Consistent Trends across Different Subjects and Architectures: Whether it’s a cat vs. a person, or a GAN vs. diffusion vs. autoregressive model, the amplitude of temporal change remains similar. **This amplitude (or trend) is precisely what motivates our design of DFactor**.
Furthermore, the sampler we use was pretrained on general content, making it adept at lower-level semantic reconstruction. This capability facilitates an effective mapping of images into the latent space for our approach.
**Q2: Superpixel Effectiveness**
Qualitative: The superpixel algorithm segments images into semantically coherent regions based on similarities in color, texture, and pixel-level low-level features. For example, human figures and backgrounds naturally form distinct semantic regions. Superpixel-based segmentation effectively decouples their individual temporal variation patterns during sampling. A detailed analysis and illustration of this benefit can be found in Appendix B (see Figure 7).
Quantitative: Experiments comparing superpixel and patch-based methods confirm improved performance. Superpixels outperform the patch-based and no-segmentation baselines by +2.04% and +3.15%. Detailed experimental results on the 12 forgery subsets are provided on anonymous link ( https://anonymous.4open.science/r/STDFD_re/README.md , if interested).
**Q3: Generalization Capability**
Qualitative: Please refer to Q1.
Quantitative: STD-FD achieves SOTA detection performance across two benchmarks involving GAN-based (DF-GAN, BGAN) and autoregressive-based models (DALLE series), supporting its general applicability.
**Q4: Mitigating Model-Target Mismatch**
Please refer to Q1.
**Q5: Diffusion Model Interchangeability**
Thanks for this practical question. Due to computational efficiency and sampling quality, we primarily use DDIM. To validate robustness, we compared DDIM with alternative sampling methods (DDPM, DPM-Solver, and Progressive Distillation):
| Method | DALLE·1 | DALLE·3 | Midjourney | Wenxin | AUC Change | Sampling Time|
|-------------|---------|---------|------------|--------|------------|-------------------|
| DDPM| 86.4 | 86.3| 89.0| 87.3 | -5.8%| ~+43%|
| DPM-Solver| 91.6| 90.7| 93.4| 95.6 | +0.3%| ~+4%|
| Progressive Distillation| 89.6| 88.3 | 92.7| 93.9 | -1.5%| ~-27%|
| DDIM (Baseline) | 91.4| 91.2| 94.0 | 93.4 | - | - | | Summary: This paper proposes an AIGC forged image detection method based on Spatio-Temporal Distribution Fitting Deviation (STD-FD). For forged images, the authors decompose the spatio-temporal features of the generation process, employ superpixel segmentation to divide semantic units, and extract the DFactor in the spatio-temporal domain by combining the noise distribution changes of the diffusion model during the denoising process. Experiments show that STD-FD outperforms existing methods on well-known datasets such as GenImage and DeepFaceGen, especially in terms of cross-generator generalization and anti-post-processing robustness.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes. The paper's core theoretical contributions are rigorously anchored in diffusion fundamentals (DDPM/DDIM frameworks), with Eq.(7) demonstrating proper alignment to established reverse process derivations.
The spatio-temporal modeling innovation (Eqs.12-14) introduces a mathematically sound mechanism for capturing temporal variation patterns via minimal-distance sampling. The discrepancy detection framework effectively operationalizes DFactors through three-dimensional feature engineering (matching, distance, correlation), forming a cohesive detection pipeline.
The theoretical scaffolding supports the empirical claims.
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes. The supplemental material reinforces methodological validity through two pillars:
(1) Theoretical grounding via DFactor pseudocode and truncated sampling visualizations that operationalize the STD-FD rationale;
(2) Empirical robustness via numerical benchmarks (AUC/ACC comparisons across 20 AIGC variants) and resource metrics (GPU memory/Running Time). The material maintains conceptual alignment with the main text while providing essential implementation transparency and scalability evidence.
Relation To Broader Scientific Literature: Proactive defense mechanisms have targeted GAN/autoregressive architectures with notable success. The text-to-image revolution driven by diffusion models, however, renders conventional reconstruction-based detection (inherited from GAN-era paradigms) increasingly inadequate.
This work transcends the "reconstruction error"[1,2,3,4] doctrine by establishing spatio-temporal distribution discrepancy modeling through diffusion sampling dynamics—a strategic alignment with cutting-edge diffusion applications in image decomposition/editing[5,6]. The paradigm shift from artifact amplification to generative process deconstruction represents advancement in next-generation AIGC defense frameworks.
Reference:
[1]“DIRE for Diffusion-Generated Image Detection”(ICCV) (2023).
[2]"AEROBLADE: Training-Free Detection of Latent Diffusion Images Using Autoencoder Reconstruction Error"(CVPR) (2024).
[3]"DRCT: diffusion reconstruction contrastive training towards universal detection of diffusion generated images"ICML(2024).
[4]"Aligned Datasets Improve Detection of Latent Diffusion-Generated Images"ICLR(2025).
[5]"SwiftEdit: Lightning Fast Text-guided Image Editing via One-step Diffusion"CVPR(2025).
[6]"Preference Alignment on Diffusion Model: A Comprehensive Survey for Image Generation and Editing"arXiv preprint arXiv(2025).
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Strengths**: This work establishes a paradigm shift in AIGC detection through spatio-temporal noise distribution dynamics analysis during diffusion sampling—a marked departure from static artifact detection. The integration of superpixel-guided semantic unit analysis with distribution fitting deviations demonstrates methodological novelty. Superior robustness is evidenced by rigorous cross-domain validation (GenImage/DeepFaceGen) against diverse generators (SD, DALL-E), coupled with deployment-friendly efficiency (Xception-level inference speed). The well-structured presentation and open-sourced implementation ensure both conceptual clarity and technical reproducibility.
**Weaknesses**：While adversarial robustness is partially validated via FGSM/PGD attacks, the evaluation lacks coverage of emerging diffusion-specific adversarial perturbations (e.g., latent space manipulation attacks). Addressing targeted attacks against diffusion sampling mechanics would strengthen real-world applicability claims.
Other Comments Or Suggestions: 1. Line 166: "Noise Reshaping" should be "Noise Normalization."
2. Line 180: "GDTW" should include a citation, as should Line 271.
3. Line 273: $match(c_k, c)$ should be $match(a_k, c_k)$.
Questions For Authors: 1. How do the parameters of superpixel segmentation (e.g., the number of blocks $K$) affect performance?
2. What is the training overhead (GPU usage and training time) of the method?
Ethical Review Flag: Flag this paper for an ethics review.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate your recognition of our method's novelty and effectiveness. Below are our responses to your Questions (Q) and Weaknesses (W):
**W: Addressing targeted attacks against diffusion sampling mechanics would strengthen real-world applicability claims.**
Thank you for your insightful feedback. Following the same experimental settings described in the "Influence of Adversarial Attacks" section, we conducted additional experiments specifically focusing on adversarial perturbations during the diffusion sampling process. Concretely, adversarial noise (with L2-norm strengths of [0.01, 0.03, 0.05]) was injected at each timestep of the reverse diffusion process (20 steps in total). Experimental results are summarized below (AUC,%):
| Perturbation | DALLE·1 | DALLE·3 | Midjourney | Wenxin | Performance |
|-----------------------|---------|---------|------------|--------|--------------------|
| 0.05 | 88.01 | 89.98 | 93.84 | 92.57 | -2.5% |
| 0.03 | 89.56 | 90.43 | 93.56 | 93.62 | -1.8% |
| 0.01 | 91.67 | 91.42 | 92.90 | 90.42 | -2.0% |
| Original (Baseline) | 91.45 | 91.20 | 94.01 | 93.48 | Baseline |
Under these adversarial conditions, the performance fluctuates within approximately 2.5%, demonstrating that the STD-FD identification mechanism remains robust against targeted sampling attacks.
**Q1: How do the parameters of superpixel segmentation (e.g., the number of blocks K) affect performance?**
Thank you for this constructive question. We performed an ablation study varying the number of superpixel blocks Kfrom the baseline setting K=10. The performance variation across different K values is within approximately 1.08%, as summarized below (AUC,%):
| K | DALLE·1 | DALLE·3 | Midjourney | Wenxin | Performance |
|----|---------|---------|------------|--------|--------------------|
| 1 | 90.46 | 90.11 | 92.89 | 92.67 | -1.08% |
| 5 | 91.45 | 90.87 | 93.76 | 94.01 | -0.01% |
| 10 (Baseline) | 91.45 | 91.20 | 94.01 | 93.48 | Baseline |
| 15 | 91.89 | 91.01 | 93.45 | 92.93 | -0.23% |
| 20 | 92.45 | 90.89 | 93.87 | 91.54 | -0.37% |
It's noteworthy that selecting a larger value of K does not always yield better results. Superpixel methods inherently suggest an optimal clustering number based on image content. In facial forgery scenario, the recommended K≈10 ensures effective semantic consistency; significantly deviating from this value negatively affects pixel-level semantic coherence and impairs spatio-temporal decoupling during diffusion sampling.
**Q2: What is the training overhead (GPU usage and training time) of the method?**
Thank you for your question. STD-FD involves diffusion sampling, DFactor construction, and downstream classification during training. The peak GPU memory usage during training is approximately 18.8GB. With a batch size of 32, the average training time per epoch is approximately 3 minutes 30 seconds (tested on NVIDIA A40 GPU with Intel Silver 4310 CPU).
**Q3: Ethical Review**
Sorry for the confusion. As stated in our Impact Statement, our research strictly targets deepfake detection, aiming to mitigate potential risks posed by generative AI technologies. We do not facilitate unethical use; rather, our work enhances reliability and security in detecting AI-generated content. Therefore, we respectfully submit that our research aligns with standard ethical guidelines.
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Rebuttal Comment 1.1:
Comment: After going through the authors' rebuttal and the other reviewers' comments, I believe my previous concerns have been fully addressed — especially with the new results on sampling perturbations, superpixel ablation studies, and practical applicability experiments. The novelty of this work remains significant, and its technical contributions are sufficiently demonstrated. I’m happy to reaffirm my recommendation to accept this paper.
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Reply to Comment 1.1.1:
Comment: Thank you sincerely for your thoughtful evaluation and encouraging feedback regarding our work! We deeply appreciate the time and care you have invested in reviewing our manuscript. We will carefully revise the manuscript accordingly. | Summary: This paper proposes STD-FD, a detection framework for AI-generated image forgeries that analyze spatio-temporal distribution deviations inherent in diffusion models' generative processes. By modeling how noise residuals evolve across temporal sampling steps and decomposing spatial patterns through superpixel segmentation, the method identifies discriminative features (DFactors) that reveal distribution mismatches between authentic and synthetic content. Unlike artifact-based approaches, STD-FD focuses on dynamic inconsistencies in the generation trajectory, achieving superior detection accuracy through systematic quantification of temporal noise propagation anomalies and localized spatial irregularities. The core innovation lies in bridging temporal modeling of diffusion behaviors with spatial forgery localization, offering a principled detection paradigm for evolving AIGC synthesis techniques.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: Yes
Experimental Designs Or Analyses: Yes
Supplementary Material: Yes. The supplementary material substantiates the paper's claims through three critical additions: (1) Pseudocode providing methodological transparency for the STD-FD framework's implementation; (2) Temporal-spatial case analyses empirically validating the core design premise of distribution deviation detection; (3) Comprehensive computational benchmarks demonstrating real-world feasibility (runtime <0.5s/image) alongside extended cross-dataset evaluations confirming generalization across diverse AIGC paradigms.
Relation To Broader Scientific Literature: The field of Deepfake detection has predominantly focused on amplifying artifacts through frequency/spatial domain transformations, while recent advances (LARE2 [CVPR'24], AEROBLADE [CVPR'24], DRCT [ICML'24]) explore image reconstruction-based paradigms.
This work innovates by addressing a critical oversight of existing end-to-end reconstruction approaches: their neglect of temporal dynamics during the reconstruction process. The key contribution lies in systematically modeling spatio-temporal distribution characteristics of genuine versus synthetic samples throughout Diffusion-based reconstruction trajectories, establishing more discriminative forgery signatures through principled analysis of generation process deviations.
Essential References Not Discussed: No
Other Strengths And Weaknesses: Strengths:
1. Detection Paradigm Innovation: By leveraging a spatio-temporal diffusion framework, this method moves beyond prior reconstruction-error-based approaches (e.g., DRCT) to systematically decompose distribution discrepancies between real and forged images.
2. Implementation Framework: Rather than simply classifying noise-variant frames end-to-end, STD-FD builds a discriminative knowledge repository via joint spatio-temporal modeling. This effectively reframes forgery detection as a feature engineering task guided by repository comparisons.
3. Experimental Validation: Large-scale tests on DeepFaceGen and GenImage demonstrate strong performance. Ablation studies, tests with mismatched pre-trained models, and resistance to adversarial attacks underscore its robustness.
4. Deployment Feasibility: The open-source release ensures reproducibility. Its lightweight distribution-matching mechanism is resource-efficient, favoring real-world deployment.
Weaknesses:
1. Is the essence of the distribution fitting bias the temporal variation in noise distribution, or is it an implicit constraint of the generative model itself? Can the authors provide further clarification?
2. A formal or axiomatic definition of DFactor should be used to delineate its core principles, further separating conceptual essence from specific implementations.
Other Comments Or Suggestions: 1. Correct "In the recent years" to "In recent years."
2. Some sentences should be restructured for clarity, e.g., "By using spatio-temporal distribution fitting deviations..." could be clearer as "Spatio-temporal distribution fitting deviations capture changes in the generative process, enabling effective forgery detection."
Questions For Authors: Please refer to the above comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you very much for your detailed review and constructive comments. We sincerely appreciate your recognition of the innovation and thoroughness of our work. Below are our responses to your Questions (Q) and Weaknesses (W):
**Q1|W1: Is the essence of the distribution fitting bias the temporal variation in noise distribution, or is it an implicit constraint of the generative model itself? Can the authors provide further clarification?**
We apologize for any confusion. The essence of the distribution fitting bias lies in the temporal variations of noise distributions. Although DDIM employs a diffusion-based architecture, we use intermediate DDIM timesteps solely to extract spatio-temporal distribution information inherent in real and forged data, rather than fitting specifically to a particular network architecture. Our experimental results provide strong evidence across two benchmarks, effectively detecting forgeries generated from different architectures, including DF-GAN and BigGAN (GAN-based) as well as the DALLE series (autoregressive-based).
**Q2|W2: A formal or axiomatic definition of DFactor should be used to delineate its core principles, further separating conceptual essence from specific implementations.**
Thank you for your valuable suggestion. We will include a formalized, abstract definition of DFactor in the final version to provide a clear conceptual paradigm beneficial to the research community.
Formally, the definition of DFactor is as follows:
> DFactor represents a feature vector derived from diffusion-based spatio-temporal decoupling, characterizing the variation patterns of specific categories. Specifically, DFactor partitions spatio-temporal information into **K** distinct classes based on feature similarity. Within each class, DFactor encodes variation patterns across superpixel regions during sampling. Consequently, these **K** classes of DFactors constitute a feature pattern library. For downstream classification tasks, relevant vectors obtained via identical spatio-temporal decoupling processes can be matched against this library to achieve precise classification.
These principles can be formalized by the following equation:
$
\mathcal{L} = -g\left(S_1(\text{DFactor}_1, \mathcal{T}_1)\, S_2(\text{DFactor}_2, \mathcal{T}_2)\,\dots\,S_K(\text{DFactor}_K, \mathcal{T}_K)\right)
$
- $\mathcal{L}$ quantifies the dissimilarity among samples across **K** categories with respect to their DFactors.
- $S_i(\text{DFactor}_i, \mathcal{T}_i)$ represents the set of distances related to a specific class $\mathcal{T}_i$.
- The function $g(\cdot)$ takes **K** finite sets as input and outputs a scalar value indicating the overall dissimilarity among these sets.
**Q3: Corrections of writing**
Thank you for your careful reading and valuable feedback. We will carefully correct these writing issues in the final version. | Summary: This work presents the Spatio-Temporal Distribution Fitting Deviation (STD-FD) method for detecting image forgery in AI-Generated Content (AIGC), specifically leveraging generative diffusion models. The authors designed DFactors, which capture deviations in temporal distribution during the diffusion process. Extensive experiments were conducted to analyze the effectiveness of the proposed method under various experimental settings.
Claims And Evidence: The paper presents two core claims.
### 1. The proposed spatiotemporal distribution extraction framework requires further examination in terms of its validity and applicability.
#### 1.1 Validity of the Method
**Overly idealized assumptions about information acquisition:**
The method assumes access to update information at each time step of the diffusion process, specifically the noise term \( \epsilon \). However, in real-world scenarios—particularly in forgery detection—such information is extremely difficult to obtain. This assumption is overly strong, as it essentially grants direct access to the complete generative process of the model. If this information were available, one could infer the model’s sampling mechanism and potentially reconstruct the generative model itself, making additional forgery detection unnecessary.
#### 1.2 Potential Overdesign of the Method
The proposed approach involves multiple steps:
- Extracting variation information between diffusion time steps.
- Identifying specific patterns within these variations.
- Performing pattern matching to detect forged images.
This process is relatively complex and may contain unnecessary design redundancies. A simpler alternative might be more feasible. For instance, if intermediate results of the diffusion process were accessible, applying downsampling or other transformations directly on these results for classification might achieve similar or even superior performance. Thus, the paper should at least include such an approach as a baseline for comparative experiments.
### 2. Recommendations for Experimental Design
Although the paper conducts extensive experiments, additional ablation studies could provide a more comprehensive evaluation of the method’s effectiveness. These include, but are not limited to:
- **Comparing with simpler baseline methods:** For example, using intermediate diffusion model outputs for classification instead of employing a complex spatiotemporal distribution extraction framework.
- **Investigating robustness across different diffusion models, sampling strategies, and acceleration techniques:** This includes comparing distilled vs. non-distilled models to assess their impact on the method’s robustness.
Methods And Evaluation Criteria: ### **Ambiguity in Task Definition**
A fundamental issue in the paper is the lack of a clearly defined task. In forgery detection, the forgery detection task can take multiple forms, such as:
- **Patch-Level Detection:** Determining whether a specific region of an image has been manipulated or forged.
- **Model Attribution:** Identifying which generative model was used to produce an entire image.
Since the paper does not explicitly specify which task the proposed method is designed for, it becomes difficult to assess the appropriateness of the method’s design and evaluation metrics. Furthermore, this ambiguity may lead to uncertainty in interpreting the experimental results, ultimately weakening the method’s applicability and generalizability.
### **Unjustified Methodological Design**
#### **Strong Assumption**
The method relies on access to intermediate time-step updates of the diffusion model, specifically \( \epsilon \). However, such information is typically unavailable in practical applications. As a result, the method is built on an overly idealized assumption, raising concerns about its feasibility in real-world forgery detection tasks.
#### **Questionable Necessity of the Method**
As previously mentioned, the proposed framework employs a complex spatiotemporal distribution extraction approach. However, more straightforward alternatives—such as directly classifying intermediate diffusion model outputs—may suffice. The paper does not provide comparative experiments to validate the relative advantages of its approach, casting doubt on the necessity of its methodological design.
### **Validity of Evaluation Metrics**
The work uses metric, such as classification AUC, which is a standard.
Theoretical Claims: The work does not make any theoretical claims and, therefore, does not include theoretical analysis.
Experimental Designs Or Analyses: ### **Issues in Experimental Analysis**
- The paper does not clearly define the specific task (e.g., **patch-level forgery detection** vs. **model attribution**). This lack of clarity makes it difficult to accurately assess the validity of the experimental design.
- As previously discussed, the method relies on an overly strong assumption—namely, access to intermediate diffusion time-step information. This assumption affects the interpretability of the experimental results.
### **Sufficiency of Experiments**
The paper conducts a large number of experiments, which is a notable strength. However, concerns remain regarding the validity of the experimental design, particularly in two key areas:
#### **Fairness of Experimental Design**
- The proposed method benefits from access to diffusion time-step information, which may provide it with an inherent advantage.
- In contrast, the baseline methods used for comparison do not have access to this information, potentially leading to an unfair comparison.
- The paper does not sufficiently discuss or address this unfairness in the experimental setup.
Supplementary Material: I have read the supplementary material, including the pseudo code and additional results.
Relation To Broader Scientific Literature: The paper focuses on a highly specific topic—**forgery detection**. The study is related to broader fields such as **trustworthy AI** and **privacy protection**.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: ### **Strengths**
1. **Large-Scale Experiments**
- The paper conducts a substantial number of experiments, demonstrating thorough empirical validation. This comprehensive experimental evaluation is a notable strength of the study.
---
### **Weaknesses**
1. **Unclear Task Definition**
- The paper does not explicitly define the specific objective of the forgery detection task. For example:
- Is the goal to detect whether a specific region of an image has been manipulated?
- Or is it to identify which generative model produced the entire image?
- The lack of task definition makes it difficult to evaluate the applicability of the proposed method.
- The paper should clearly specify **which specific task the method is designed for** and **justify the choice of this task**.
2. **Strong Assumption on Accessibility of Intermediate Diffusion Steps**
- The method assumes **access to intermediate time-step information of the diffusion process (e.g., \(\epsilon\) updates)**, which is typically **unavailable in real-world forgery detection scenarios**.
- In practice, forgery detection usually relies on analyzing the final synthesized image without access to the generative process.
- The paper should **justify the validity of this assumption** or explore the feasibility of the method **without this assumption**.
3. **Potential Overdesign of the Method**
- The proposed framework involves **a complex spatiotemporal variation extraction pipeline**, including:
- Computing similarity across different time steps.
- Analyzing changes in similarity over time.
- Identifying patterns in these changes.
- Matching patterns with images using gradient descent.
- This multi-step process introduces extra computational complexity and potential design redundancies.
- **Lack of Exploration of Simpler Alternatives**:
- If intermediate diffusion steps are accessible, why not directly use these frames with downsampling?
- The paper should:
- **Analyze the computational complexity of the method**.
- **Compare the proposed approach with simpler alternatives** to demonstrate its necessity.
4. **Unclear Justification for Spatial Information Extraction Strategy**
- The method extracts spatial information using a **superpixel-based approach** instead of a more conventional **patch-based** method.
- The paper may clarify:
- **Why was the superpixel approach chosen over simpler patch-based methods?**
- **Has the effectiveness of different spatial extraction strategies been compared?**
5. **Uncertainty in the Method’s Generalizability Across Different Diffusion Sampling Strategies**
- The method relies on intermediate updates within the diffusion process, but its effectiveness under different sampling strategies remains unclear.
- **Potential Factors Affecting Performance**:
- **Variation in sampling steps across models** (e.g., Model A samples in 10 steps, while Model B samples in 5).
- **Differences in ODE-based solvers** (e.g., DDIM vs. DPM-Solver).
- **Applicability to stochastic sampling methods** (e.g., the paper adopts a deterministic approach like DDIM—does the method work with stochastic sampling?).
- **Effectiveness on distilled diffusion models**.
- The paper does not explore these concerns and should:
- **Conduct experiments to analyze the method’s robustness across different sampling strategies, step counts, and diffusion models**.
- **Discuss the impact of various sampling techniques on the method’s effectiveness**.
Other Comments Or Suggestions: Typos in Eq. 15.
Questions For Authors: 1. **What specific forgery detection task is the method designed for?**
- Is the goal to detect local manipulations within an image or to attribute the image to a specific generative model?
- What is the motivation behind choosing this particular task?
2. **How does the method remain feasible without access to intermediate diffusion steps?**
- Given that real-world forgery detection scenarios do not typically provide access to diffusion process updates (e.g., \(\epsilon\)), how can the method be adapted to work without this assumption? Is there empirical evidence supporting the validity of this assumption?
3. **Why is the proposed method designed with such a complex multi-step framework?**
- What advantages does this pipeline offer over simpler alternatives (e.g., direct classification using intermediate diffusion outputs with downsampling)? Has the computational complexity been analyzed to justify the need for each step?
4. **Why was a superpixel-based approach chosen for spatial information extraction?**
- How does it compare to a more conventional patch-based method?
5. **How well does the method generalize across different diffusion sampling strategies?**
- Does the method perform consistently when applied to diffusion models with varying step counts, solvers (e.g., DDIM vs. DPM-Solver), or stochastic sampling approaches?
- Is the method still effective when used with distilled diffusion models?
- Have experiments been conducted to assess the robustness of the approach under different sampling conditions?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for acknowledging our work. **However, there is a significant misunderstanding: we do not use intermediate steps from the forgery generation architecture (Model A). Instead, we employ a general diffusion model (Model B) to obtain its intermediate process. Without knowing the specific architecture used for generating fake images, we map the images into a latent space and model the spatio-temporal distribution based on that latent temporal information**. Below are responses to your questions (Q) and weaknesses (W):
**Q1/W1: Clarification on Task Definition**
Apologize for any ambiguity. Our work focuses on binary image authenticity detection by disentangling spatio-temporal distribution differences between real and synthetic images. This is achieved through analyzing time-step noise patterns via DDIM sampling (unrelated to forgery generation).
**Q2/W2: Assumption on Intermediate Diffusion Information & Experimental Fairness**
Sorry for the misunderstanding. We clarify that no assumptions are made regarding access to original generative models (Model A). Instead, our framework uses publicly available DDIM sampling (Model B) to capture temporal noise dynamics. As illustrated in Figure 1a, STD-FD integrates the sampling process natively, ensuring practical applicability. The acquisition of intermediate diffusion features constitutes our key innovation rather than an unfair experimental advantage.
**Q3/W3: Alternative Methods & Complexity**
Sorry for the confusion.
a) Upon initially discovering the importance of temporal sampling differences, we indeed experimented with simpler alternatives. Initial experiments with 3D-Xception and ViT achieved 87.48% and 88.01% AUC on DeepFaceGen – comparable to SOTA but below our method. The key improvement is the careful decoupling of temporal discrepancies, inspiring the fine-grained design of our STD-FD approach centered around the DFactor module.
b) STD-FD requires 272ms (2253MiB) per image (Line 761), comparable to Xception (253ms/2090MiB) and EfficientNet (241ms/1985MiB).
**Q4/W4: Superpixel vs. Patch-based**
Thanks for your question.
Qualitative: Superpixel segments images into regions with similar color, texture, and low-level features, producing blocks more consistent with pixel-level semantics than uniform grid partitioning. Such spatial processing is essential for effectively decoupling temporal noise maps. For example, superpixel segmentation can distinguish distinct temporal variation patterns between human subjects and backgrounds, as detailed in Appendix B (Figure 7 for a specific case analysis).
Quantitative: Our ablation study demonstrates that superpixels outperform the patch-based and no-segmentation baselines by +2.04% and +3.15% AUC, respectively. Detailed experimental results on the 12 forgery subsets, following the guidelines of this rebuttal, are provided on an anonymous link (if interested: https://anonymous.4open.science/r/STDFD/README.md ).
**Q5/W5: a) Experiments with different sampling conditions; b) Sampling steps; c) Sampling methods**
Appreciate your advice.
a) Yes, Influence of sampling steps (line 416) show improved detection performance with increasing timesteps (from T=5 to 50). Notably, even at T=5, the AUC surpassed 90%, outperforming SOTA. This underscores the efficacy of modeling forgery traces via spatio-temporal distributions.
b) Please see a).
c) We incorporated additional sampling methods, including DDPM, DPM-Solver, and Progressive Distillation. Experiments followed the identical setup used in the influence of sampling steps study (line 416):
- Reverse process of DDPM involves a stochastic Markov chain with randomness at each step. With limited steps, noise errors accumulate significantly, reducing the quality and efficiency of spatio-temporal features compared to deterministic methods (ideal results require around 1000 steps).
- DPM-Solver reformulates diffusion sampling as solving an ODE using higher-order solvers, providing excellent image reconstruction quality in just 20 steps. Although high-quality outputs and superior FID scores are achieved, computational overhead inevitably increases due to the higher-order ODE solution.
- Progressive Distillation (PD) utilizes pretrained DDIM as teacher model, training a student model to mimic the teacher’s performance in fewer steps. Although sampling times significantly decrease, a performance drop of 1.5% is observed due to changing the optimization objective.
| Method | DALLE·1 | DALLE·3 | Midjourney | Wenxin | AUC Change | Sampling Time|
|--------------|---------|---------|------------|--------|------------|---------------------|
| DDPM| 86.4| 86.3| 89.0| 87.3| -5.8%| ~+43%|
| DPM-Solver| 91.6| 90.7| 93.4| 95.6| +0.3% | ~+4%|
| PD| 89.6| 88.3| 92.7| 93.9| -1.5%| ~-27%|
| DDIM (Baseline) | 91.4| 91.2| 94.0| 93.4 | - | - |
**W6: Equation Corrections**
Thanks for meticulous review. We will rectify all notation inconsistencies in the final version. | null | null | null | null | null | null |
Simple Policy Optimization | Accept (poster) | Summary: This paper theoretically identifies a flaw of the clipping technique in PPO's objective and proposes a solution to it. Empirical results show that the proposed solution achieves comparable or better performance on MuJoCo and Atari, and the performance improves as the policy network scales.
Claims And Evidence: The abstract claims that TRPO has a strong theoretical foundation while PPO has better practical efficiency, and that the proposed method achieves the best of both worlds. This sounds a bit odd because from the empirical results the proposed method actually performs better than PPO (this is even stated at the end of the abstract).
Methods And Evaluation Criteria: Yes.
Theoretical Claims: No, I did not.
Experimental Designs Or Analyses: Figure 10: The results on Atari are averaged over only 3 random seeds, which I think is not sufficient.
Supplementary Material: Yes, all of them.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: - The theoretical explanation of why PPO's clipping technique may not be optimal is convincing, and the corresponding illustration in Figure 2 is intuitive.
- The implementation of the proposed method is simple.
- The empirical performance of the proposed method is strong, especially on Atari tasks. The fact that the performance improves as the network scales is particularly promising.
Other Comments Or Suggestions: The results in Figure 8 look stronger than the MuJoCo results and would be better if put in the main paper instead of the appendix.
Questions For Authors: - Could you specify which implementation of PPO you are using (which implementation SPO is based on)? I am a little concerned since as also pointed out by this paper, existing work has shown that the performance of PPO is highly dependent on code-level optimization. It would be better if the url of the implementation is included in the paper.
- Have you tried scaling the width of the network besides the depth? I'm curious because a recent paper has shown that scaling the width can yield significant performance improvements on its own \[1\].
- Do you have any idea why PPO tends to perform worse and lose control of the probability ratio as the network scales?
- Could you show the scaling performance in Atari? It would be more convincing if there are multiple benchmarks where the results support the claim.
- Figure 2 (right): Could you specify the task on which the results are produced?
\[1\] Obando-Ceron et al., "In value-based deep reinforcement learning, a pruned network is a good network".
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer uY8N,
Thank you for your positive feedback. Below, we will address your concerns.
>Figure 10: The results on Atari are averaged over only 3 random seeds, which I think is not sufficient.
Thank you for your suggestion. Given the high computational costs associated with Atari environments, the use of 3 random seeds represents a well-established practice in the field [2]. Furthermore, due to time constraints during the rebuttal period, we regret that we are unable to conduct additional experiments with more random seeds.
>The results in Figure 8 look stronger than the MuJoCo results and would be better if put in the main paper instead of the appendix.
Thank you for your suggestion! Due to space constraints, we have included the key content in the main text (Figure 4 compares a broader range of baselines). If the paper is accepted, we will also incorporate Figure 8 into the main body.
>Could you specify which implementation of PPO you are using (which implementation SPO is based on)?...
Our implementation of PPO is based on the standard CleanRL library: https://github.com/vwxyzjn/cleanrl, with the only modification being the computation of the policy loss in SPO. The complete code for this study has been submitted as part of the **supplementary materials**.
>Have you tried scaling the width of the network besides the depth? I'm curious because a recent paper has shown that scaling the width can yield significant performance improvements on its own [1].
Thank you for the additional paper. Our three-layer network follows the default settings: [$\mathrm{dim}(\mathcal{S})$, 64, 64, $\mathrm{dim}(\mathcal{A})$], while the seven-layer network is both deeper and wider in architecture: [$\mathrm{dim}(\mathcal{S})$, 256, 256, 128, 128, 64, 64, $\mathrm{dim}(\mathcal{A})$].
>Do you have any idea why PPO tends to perform worse and lose control of the probability ratio as the network scales?
Certainly! We'd be happy to provide a simplified explanation. Generally speaking, deeper networks tend to have larger Lipschitz constants, meaning that even minor changes in the network's input can lead to significant variations in its output. Consequently, when using deeper architectures, PPO's limitations become more pronounced, as slight parameter adjustments may cause the probability ratio to exceed its boundary.
>Could you show the scaling performance in Atari? It would be more convincing if there are multiple benchmarks where the results support the claim.
Thank you for your suggestion. We primarily demonstrate the scaling performance in Atari environments through Figures 1 and 6. Specifically, Figure 1 shows that SPO can effectively train ResNets with over 100 layers, while Figure 6 highlights SPO's significant performance improvements using ResNet-18 across four Atari environments.
Additionally, due to the limited rebuttal period, we may require additional time to obtain the Atari results, potentially during the discussion phase.
>Figure 2 (right): Could you specify the task on which the results are produced?
Sure! We generated Figure 2 using the Hopper-v4 environment. In fact, similar results can be reproduced in any environment (e.g., Humanoid-v4).
Best,
Authors
---
*Reference:*
[1] J Obando-Ceron et al. In value-based deep reinforcement learning, a pruned network is a good network.
[2] Y Gan et al. Reflective policy optimization. | Summary: This paper introduces Simple Policy Optimization (SPO), a first-order algorithm that modifies PPO's policy loss to achieve stronger theoretical properties, particularly in bounding the probability ratios between successive policies. The authors argue that by optimizing a lower bound under TV divergence constraints, SPO provides a more effective solution space than approaches using KL divergence (e.g., TRPO). Empirical results show that SPO performs comparably to PPO across some benchmarks.
Claims And Evidence: Partially. The claim regarding improved theoretical properties is plausible, but empirical support for SPO’s superiority over PPO and TRPO is limited.
Methods And Evaluation Criteria: Yes, the methods are appropriate for policy optimization tasks, though additional experiments would strengthen the evaluation.
Theoretical Claims: While the high-level ideas of the theorem seem sound, the integration into the overall argument could be clearer.
Experimental Designs Or Analyses: Experimental designs are reasonable but lack robustness due to a small number of seeds and limited hyperparameter tuning discussions.
Supplementary Material: Yes, I have reviewed the supplementary materials.
Relation To Broader Scientific Literature: Builds upon PPO and TRPO, addressing known issues with PPO's trust region enforcement.
Essential References Not Discussed: No.
Other Strengths And Weaknesses: **Strengths**
- Proposes a modification to the PPO objective that aims to provide stronger theoretical guarantees.
- Provides theoretical analysis comparing different divergence constraints and their impact on policy optimization.
- Experimental validation includes several benchmark environments, which help illustrate the method’s potential in diverse tasks.
**Weaknesses**
- The paper lacks a clear demonstration of significant performance improvements over PPO, with most experimental results showing only marginal gains.
- Claims regarding the theoretical advantages of SPO over PPO and TRPO are not fully substantiated with rigorous empirical validation.
- Key implementation details and hyperparameters (e.g., the reasoning behind comparing 3-layer vs. 7-layer architectures) are insufficiently explained. This makes it difficult to assess whether the results stem from algorithmic improvements or implementation choices.
- Several experimental setups (e.g., Figure 6) lack clarity in terms of legend explanations and parameter settings. Additionally, the small number of random seeds (only three) undermines the statistical robustness of the results.
Other Comments Or Suggestions: - In the experiments, provide more details on architectural choices (e.g., why 3-layer and 7-layer networks were compared). Discuss whether the variations in performance are due to SPO or other factors.
- Include a comparison with TRPO, as the paper suggests that SPO combines the advantages of both TRPO and PPO. A head-to-head comparison would strengthen this claim.
- Provide clearer explanations in the captions of Figures 5, 6, and 7. For example, explain what the numeric values in the legends (e.g., 0.1, 0.2) represent and clarify the meaning of horizontal lines.
- Expand the experimental evaluation to include more random seeds (at least 10) to enhance the reliability of the results.
Questions For Authors: Q1. How do the proposed SPO results compare directly with TRPO across the same benchmarks? Can you provide experimental comparisons to clarify this?
Q2. Is there a tunable parameter in SPO that allows interpolation between PPO-like and TRPO-like behavior? If so, how does varying this parameter affect performance?
Q3. What is the meaning of the values shown in the legends of Figures 5 and 6 (e.g., 0.1, 0.2)? If these values represent $\epsilon$, how is $\epsilon$ specifically related to the ResNet architecture and not to other settings? What do the horizontal lines in these figures represent?
Q4. Can you clarify the meaning of Theorem 5.1 (that SPO is $\epsilon$-aligned)? How does this translate into practical advantages in policy optimization?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer eeAe,
Thank you for your constructive feedback. Below, we will address your concerns.
>Partially. The claim regarding improved theoretical properties is plausible, but empirical support for SPO’s superiority over PPO and TRPO is limited.
>The paper lacks a clear demonstration of significant performance improvements over PPO, with most experimental results showing only marginal gains.
>Include a comparison with TRPO, as the paper suggests that SPO combines the advantages of both TRPO and PPO. A head-to-head comparison would strengthen this claim.
Thank you for your suggestion. However, as demonstrated in Figures 1, 4, and 5 of our paper, our experiments show that SPO indeed exhibits significant advantages over PPO. Notably, Figure 4 includes comparisons with **a wide range of baselines**. Unfortunately, due to TRPO's computationally expensive second-order optimization, it is typically not used as a baseline in existing works [1, 2, 3].
>Claims regarding the theoretical advantages of SPO over PPO and TRPO are not fully substantiated with rigorous empirical validation.
Thank you for your feedback. As shown in Table 1 of our paper, when PPO trains deeper networks, the probability ratio becomes uncontrolled and leads to performance collapse in PPO. Please note that in this experiment, the only variable modified was the network depth - no additional code-level tuning was performed for SPO. We believe this strongly demonstrates SPO's theoretical advantage, as its probability ratio remains effectively constrained without performance degradation even with increasing network depth.
>Key implementation details and hyperparameters (e.g., the reasoning behind comparing 3-layer vs. 7-layer architectures) are insufficiently explained...
>In the experiments, provide more details on architectural choices (e.g., why 3-layer and 7-layer networks were compared)...
Thank you for your suggestion. The reviewer's concern primarily relates to the fairness of the experimental setup and the potential possibility that SPO might involve additional hyperparameters or code-level tuning. Regarding this point, please refer to our already uploaded SPO and PPO implementations, where you will find that the only difference between SPO and PPO lies in the policy loss computation (the sole modification in the trainer.py file, with all other settings remaining identical).
As for the network depth selection, we employed both the default three-layer mlp [$\mathrm{dim}(\mathcal{S})$, 64, 64, $\mathrm{dim}(\mathcal{A})$] and a randomly selected seven-layer mlp [$\mathrm{dim}(\mathcal{S})$, 256, 256, 128, 128, 64, 64, $\mathrm{dim}(\mathcal{A})$] to ensure comprehensive evaluation.
>Several experimental setups (e.g., Figure 6) lack clarity in terms of legend explanations and parameter settings. Additionally, the small number of random seeds (only three) undermines the statistical robustness of the results.
Thank you for your careful review. In Figure 6, the red dashed line represents the value of 0.2, while all other elements are clearly indicated in the legend.
Regarding the random seeds, due to the computational costs in Atari environments, using 3 seeds is a common choice [4]. Furthermore, for the MuJoCo environments, the results presented in Figure 4 were indeed obtained using 10 random seeds to ensure statistical reliability.
>Q2. Is there a tunable parameter in SPO that allows interpolation between PPO-like and TRPO-like behavior?...
Please note that TRPO and PPO exhibit fundamentally different optimization behaviors. SPO combines TRPO's theoretical guarantee (monotonic improvement) with PPO's computational efficiency (eliminating the need for second-order optimization).
>Q3. What is the meaning of the values shown in the legends of Figures 5 and 6 (e.g., 0.1, 0.2)?...
The red dashed lines in these figures represent the hyperparameter epsilon (typically set to 0.2), and we will add the corresponding legend in subsequent revisions. The remaining horizontal lines, which are already labeled in the legend, indicate the performance of the original CNN at convergence (serving as baseline references).
>Q4. Can you clarify the meaning of Theorem 5.1 (that SPO is $\epsilon$-aligned)? How does this translate into practical advantages in policy optimization?
Please refer to the performance improvement lower bound (10). Theorem 5.1 demonstrates that SPO can indirectly optimize this lower bound (10) by constraining the probability ratio deviation $\|\frac{\tilde{\pi}(a|s)}{\pi(a|s)}-1\|\leq\epsilon$.
Best,
Authors
---
*Reference:*
[1] K Cobbe et al. Leveraging procedural generation to benchmark reinforcement learning.
[2] Y Wang et al. Truly proximal policy optimization.
[3] Y Wang et al. Trust region-guided proximal policy optimization.
[4] Y Gan et al. Reflective policy optimization.
---
Rebuttal Comment 1.1:
Comment: Thanks to the authors for the response.
Reiterating my concerns regarding architecture choice:
What is the rationale behind comparing 3-layer versus 7-layer architectures? I’m still unclear on why a particular choice of architecture might favor SPO over others—either from a theoretical or empirical standpoint. For instance, in Figure 5 (Ant-v4), PPO with a 3-layer architecture outperforms all other settings, including SPO with both 3 and 7 layers. However, SPO with 7 layers performs better than PPO with 7 layers. Similar trends appear in other environments depicted in Figure 5. While these are certainly interesting empirical findings, is there any theoretical justification or further insight into why SPO might perform better under certain architectural configurations?
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer eeAe,
Thank you for your additional comments. Below, we will address your concerns.
We did not deliberately choose the network architecture or depth; the primary motivation of the experiment was to reveal that PPO **fails to constrain the probability ratio**. To explain why network depth (or, more generally, network complexity) can make this phenomenon more pronounced, we provide the following insights:
According to the empirical results in [1], the default policy network used in the MuJoCo is [$\mathrm{dim}(\mathcal{S})$, 64, 64, $\mathrm{dim}(\mathcal{A})$], which is a network structure with fairly limited capacity. As the network becomes deeper (or wider), small changes in parameters can lead to large variations in output. When training neural networks with a larger number of parameters, PPO’s clipping mechanism causes some data to have zero gradients. Due to the large number of parameters, the proportion of data that actually contributes to gradients during PPO's training **decreases faster compared to shallower networks**. This leads to larger bias in the data that provides gradients, ultimately pushing the policy entirely out of the trust region and resulting in performance collapse.
SPO addresses this issue because each data point in SPO provides a gradient directed toward the constraint boundary. As a result, data points that attempt to escape the trust region are pulled back by the gradient, thereby enforcing the trust region constraint more effectively and leading to stable performance improvements.
To illustrate this, we further conducted the following experiment, where the policy network was set to
[$\mathrm{dim}(\mathcal{S})$, 256, 256, 256, $\mathrm{dim}(\mathcal{A})$] and [$\mathrm{dim}(\mathcal{S})$, 512, 512, 512, $\mathrm{dim}(\mathcal{A})$]
to rule out the possibility that SPO's performance benefits from a specific network architecture. The results are as follows:
**Policy network: [$\mathrm{dim}(\mathcal{S})$, 256, 256, 256, $\mathrm{dim}(\mathcal{A})$]**
| Algorithm | Ant-v4 | Humanoid-v4 | HumanoidStandup-v4 |
|--------|-----|------|------|
| PPO | $-58.73\pm57.06$| $513.8\pm49.02$| $72210.81\pm10491.1$ |
| SPO | $4048.64\pm1045.12$| $2504.07\pm981.37$ |$149694.08\pm20166.95$ |
**Policy network: [$\mathrm{dim}(\mathcal{S})$, 512, 512, 512, $\mathrm{dim}(\mathcal{A})$]**
| Algorithm | Ant-v4 | Humanoid-v4 | HumanoidStandup-v4 |
|--------|-----|------|------|
| PPO | $-36.58\pm31.42$| $580.09\pm39.65$| $77964.68\pm14870.27$ |
| SPO | $2278.72\pm751.46$| $1971.7\pm919.23$ |$155631.11\pm23507.7$ |
We can see that as the network parameter increases, PPO can not learn a good policy, whereas SPO is still able to perform well. We also demonstrate the **average and maximum ratio deviation** of PPO and SPO during the training process under these two network structures:
**Policy network: [$\mathrm{dim}(\mathcal{S})$, 256, 256, 256, $\mathrm{dim}(\mathcal{A})$]**
| Algorithm | Ant-v4 | Humanoid-v4 | HumanoidStandup-v4 |
|--------|-----|------|------|
| PPO | $6.31(4264.61)$| $24.15(22444.92)$| $28.77(34402.84)$ |
| SPO | $0.16(0.29)$| $0.16(0.22)$ |$0.16(0.2)$ |
**Policy network: [$\mathrm{dim}(\mathcal{S})$, 512, 512, 512, $\mathrm{dim}(\mathcal{A})$]**
| Algorithm | Ant-v4 | Humanoid-v4 | HumanoidStandup-v4 |
|--------|-----|------|------|
| PPO | $5.55(3536.7)$| $30.9(41786.79)$| $48.98(241293.98)$ |
| SPO | $0.17(0.28)$| $0.17(0.2)$ |$0.17(0.21)$ |
It can be observed that as the number of network parameters increases, PPO **fails to constrain the probability ratio deviation**, with its maximum value reaching an astonishing **240,000** in the HumanoidStandup-v4 environment. In contrast, regardless of changes in the network structure, SPO's probability ratio deviation remains very stable and stays below the hyperparameter threshold $\epsilon=0.2$. This fully demonstrates that SPO's outstanding performance does not benefit from a specific network architecture but is capable of **consistently constraining the probability ratio**—and thus stabilizing training—under any network settings.
Finally, thank you for your constructive feedback on our paper. As this is our final response, if all your concerns have been addressed, we would sincerely appreciate your stronger support (i.e., higher rating) for our paper. Thank you very much!
Best,
Authors
---
*Reference:*
[1] S Huang et al. The 37 implementation details of proximal policy optimization. | Summary: The paper introduces Simple Policy Optimization (SPO), a new unconstrained first-order reinforcement learning algorithm designed to effectively combine strengths from Trust Region Policy Optimization (TRPO) and Proximal Policy Optimization (PPO). SPO modifies PPO's objective by proposing a novel surrogate loss that constrains the probability ratio using Total Variation (TV) divergence, theoretically enhancing policy improvement. Empirical evaluations on Atari and MuJoCo benchmarks suggest SPO can achieve better or comparable performance than PPO, particularly when training deeper neural networks.
### Update After Rebuttal
I appreciate the authors’ response. However, none of my concerns have been adequately addressed.
**Regarding Theorem 4.3 and the associated conclusion:**
It appears that the authors misunderstood the core of my concern. My point is that Theorem 4.3 does *not* support the claim that "TV can lead to better policy improvement." What is actually shown is that the surrogate objective with TV is greater than that with KL, i.e., $L(\pi_{\text{TV}}) \ge L(\pi_{\text{KL}})$. This does not imply that the *true* performance of the final policy is better, i.e., $\eta(\pi_{\text{TV}}) \ge \eta(\pi_{\text{KL}})$. Additionally, Equation (3) should not include a constraint, as the surrogate objective itself does not include one.
**Regarding the rigor of Equations 17–18:**
What I am asking for here is a formal and rigorous proof. I am concerned that the method may be biased due to the added term, and this needs to be clarified with a precise derivation.
**On experimental sufficiency:**
As I previously noted, even adding a random component can result in performance improvements on half of the 57 Atari games. The current experimental evidence is therefore not sufficient to substantiate the paper’s claims.
Given the above concerns, I will maintain my original score. The paper itself may introduce some potential alternative solution to PPO. I hope the author polish their theories and enhance their experiments.
Claims And Evidence: The main claims—that SPO achieves superior policy improvement by effectively bounding probability ratios using TV divergence—are inadequately supported by the presented evidence. Specifically, the theoretical claim that "TV divergence offers a larger solution space than KL divergence" is problematic. The provided proofs confuse constraint-based optimization (eq. 13) and surrogate objective-based optimization (eq. 16). Consequently, the statement that TV constraints yield a "more effective solution space" than KL constraints lacks convincing support and clarity. Additionally, the step from eq. (17) to (18) and the treatment of the absolute advantage versus squared difference are neither adequately justified nor analyzed.
Please also see Theoretical Claims for more detail.
Methods And Evaluation Criteria: In my understanding, the proposed approach differs from PPO with KL Penalty primarily in two aspects:
- It replaces the KL divergence with alternative divergence terms.
- It introduces an absolute value of the advantage term into the adaptive coefficient.
Therefore, a comparison with this PPO variant would be necessary to clearly demonstrate whether using TV divergence provides any advantage over KL divergence.
Theoretical Claims: Q 1:
The paper contains several clear theoretical and logical errors.
The authors claim that "TV divergence offers a larger solution space compared to methods incorporating a looser KL divergence constraint." However, the fundamental issue is that when optimizing the surrogate objective loss, the paper does not actually enforce a KL divergence constraint. Specifically, in equation (13), restricting the solution space to $\tilde{\pi} \in \Omega_{TV}$ is incorrect. The authors seem to have confused constraint-based optimization objectives with surrogate loss-based objectives.
Consequently, their conclusion that "Optimizing the lower bound with TV divergence constraints offers a more effective solution space than using KL divergence constraints, leading to better policy improvement" is incorrect.
To clarify this rigorously, if the authors wish to demonstrate that surrogate objective $A$ is superior to surrogate objective $B$, they must:
- Remove artificial restrictions on the solution space, such as $\tilde{\pi} \in \Omega_{TV}$.
- Provide a formal proof showing $\eta(\pi^*_A) \geq \eta(\pi^*_B)$ rather than relying solely on comparisons using the surrogate loss $\mathcal{L}$.
Q 2:
The derivation from Eq. (17) to Eq. (18) does not appear rigorous. Specifically, replacing the absolute value $|r - 1|$ with the squared term $(r - 1)^2$ significantly changes the nature of the function. The paper lacks an analysis of the divergence introduced by this transition from Eq. (17) to Eq. (18). Additionally, it is unclear whether this modification will lead to actual policy performance improvements.
Q 3:
Definition 5.1 does not appear clearly motivated or sufficiently rigorous. The notion of an "$\epsilon$-aligned" surrogate is not strong enough to guarantee policy improvement. In fact, many surrogate functions can satisfy the condition of being "$\epsilon$-aligned" yet fail to yield any meaningful performance improvement. Therefore, the practical usefulness and theoretical significance of this definition remain unclear.
Experimental Designs Or Analyses: The experimental analyses have limitations. The selection of only 35 out of 57 Atari environments raises concerns about potential cherry-picking or hyperparameter sensitivity. The inconsistent results between Figure 1 and Figure 8 suggest sensitivity to hyperparameters, not robustness.
Additionally, the inconsistent performance of PPO-Penalty regarding median metrics versus optimality gaps requires further clarification. Moreover, the method "PPO-Penalty" itself is not clearly defined in the paper; I could not find any explicit definition or description provided.
Finally, deeper network experiments compared only to PPO are insufficient to demonstrate the generality of the proposed method; comparisons to additional baselines are required.
Supplementary Material: Supplementary materials have been reviewed, particularly focusing on extended experimental results and hyperparameter settings, which are clear but insufficient to clarify theoretical concerns.
Relation To Broader Scientific Literature: The paper appropriately situates itself within the literature of TRPO and PPO improvements. However, th theoretical contributions claimed, especially regarding TV versus KL divergence, must be more clearly contextualized with respect to existing results on divergence constraints in reinforcement learning literature.
Essential References Not Discussed: Further discussion and comparison with PPO using a KL penalty would be beneficial.
Other Strengths And Weaknesses: Strengths include the simplicity of the SPO objective and promising empirical results for deeper neural networks. Weaknesses center primarily around theoretical ambiguities, insufficient comparative analysis, and questionable hyperparameter sensitivity.
Other Comments Or Suggestions: - Formulations can be streamlined for clarity; currently, some equations are unnecessarily repeated or redundant.
- Theorem 3.1 is not actively used and does not aid in understanding the proposed SPO method; it could be omitted or properly integrated.
Questions For Authors: 1. Can you rigorously justify why the absolute deviation (eq. 18) is preferred over squared deviation, given significant conceptual differences?
2. How do you explain the contradictory performances of SPO in Figures 1 and 8?
3. What are the detailed reasons for selecting only 35 out of the 57 available Atari environments, and how were these environments chosen?
4. Could you explicitly compare the performance of SPO with PPO-penalty, clearly identifying whether TV divergence or other modifications provide the primary benefit?
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Dear Reviewer 8JyT,
Thank you for your comment. Below, we will address your concerns.
>The authors claim that "TV divergence offers a larger solution space compared to methods incorporating a looser KL divergence constraint." However, the fundamental issue is that when optimizing the surrogate objective loss, the paper does not actually enforce a KL divergence constraint. Specifically, in equation (13), restricting the solution space to $\tilde{\pi}\in\Omega_ {\mathrm{TV}}$ is incorrect. The authors seem to have confused constraint-based optimization objectives with surrogate loss-based objectives.
Thank you for your comment. However, we respectfully disagree with this perspective. In our approach, we introduce the SPO objective in Equation (16) to constrain the probability ratio, thereby ensuring the $\epsilon$-aligned property defined in Definition 5.1. Furthermore, as established in Equation (9), constraining the probability ratio across batch data inherently bounds the total variation (TV) divergence, which naturally leads to a TV divergence-based trust region. Importantly, Theorem 4.3 demonstrates that the performance improvement lower bound under TV divergence constraints is indeed superior to that under KL divergence constraints.
>The derivation from Eq. (17) to Eq. (18) does not appear rigorous. Specifically, replacing the absolute value $|r-1|$ with the squared term $(r-1)^2$ significantly changes the nature of the function. The paper lacks an analysis of the divergence introduced by this transition from Eq. (17) to Eq. (18). Additionally, it is unclear whether this modification will lead to actual policy performance improvements.
>Definition 5.1 does not appear clearly motivated or sufficiently rigorous. The notion of an "$\epsilon$-aligned" surrogate is not strong enough to guarantee policy improvement. In fact, many surrogate functions can satisfy the condition of being "$\epsilon$-aligned" yet fail to yield any meaningful performance improvement. Therefore, the practical usefulness and theoretical significance of this definition remain unclear.
>Can you rigorously justify why the absolute deviation (eq. 18) is preferred over squared deviation, given significant conceptual differences?
This might be a misunderstanding of our method. We employ the squared penalty because it is convex with respect to the probability ratio $r$, and its optimal solution naturally lies at the probability ratio boundary $r^*=1+\mathrm{sign}(A)\cdot\epsilon$. This demonstrates our method's effectiveness in constraining the probability ratio, which consequently leads to indirect optimization of the policy's performance improvement lower bound (10).
>How do you explain the contradictory performances of SPO in Figures 1 and 8?
Please note that Figure 1 presents results using 50 to 101-layer ResNet architectures, while Figure 8 employs the default shallow CNN structure for comparison.
>What are the detailed reasons for selecting only 35 out of the 57 available Atari environments, and how were these environments chosen?
We deliberately selected a subset of Atari environments where PPO can operate successfully. Among the 57 Atari games, some involve sparse reward settings where neither PPO nor SPO can effectively train reinforcement learning policies. Furthermore, given the substantial computational overhead of Atari experiments, running all environments would be prohibitively time-consuming. We maintain that the environments included in our experiments provide sufficient basis for meaningful algorithmic comparison.
>Could you explicitly compare the performance of SPO with PPO-penalty, clearly identifying whether TV divergence or other modifications provide the primary benefit?
Thank you for your suggestion. Figure 4 in the paper includes comparative experiments between PPO-Penalty and other extensive baselines, with the results clearly demonstrating SPO's performance advantages over both PPO-Clip and PPO-Penalty in MuJoCo environments (10 seeds).
Best,
Authors | Summary: This paper studies an alternative of PPO, named Simple Policy Optimization (SPO), by optimizing a tighter performance lower bound using Total Variation (TV) divergence. The authors are concerned with PPO’s limitation in constraining probability ratios, which is an important problem to study.
Claims And Evidence: Most claims are well supported.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: I checked the theories that show the properties of the proposed method but did not check the derivation in previous sections.
Experimental Designs Or Analyses: Yes, the experimental designs are valid. However, it would make the results more convincing and interesting if the following problems were also studied:
1. PPO is widely used in large-scale RL problems, and KL regularization will be incorporated when the policy NN is complex, such as LLM. By doing so, the concerned limitation of PPO in constraining probability ratios would not be a problem and hardly to be observed in practice. Can the authors compare the above PPO variant and SPO? It would be great if the experiment could be completed for more complex NNs, such as LLM alignment or reasoning. The studied 7-layer MLP is still not deep enough to claim SPO's robustness in larger-scale settings.
2. Another interesting ablation will be to decrease PPO's $\epsilon$ or increase SPO's $\epsilon$ so that their average ratio deviation is the same and see if the ratio is the main reason for SPO's better performance.
3. An ablation on SPO's $\epsilon$ will help the readers better understand its robustness.
Supplementary Material: Yes, I cheked the experimental results.
Relation To Broader Scientific Literature: This paper is related to PPO and other zeroth-order policy gradient methods.
Essential References Not Discussed: The paper [1] also studies replacing the divergence term to TV divergence but is not discussed.
[1] Chu et al. "A Strong On-Policy Competitor To PPO."
Other Strengths And Weaknesses: Strengths: 1. The paper is clearly written and easy to follow.\
2. The paper has a good motivation.
Weaknesses: 1. The related works that use TV divergence or more general divergence are not thoroughly discussed.\
2. The experimental results and ablations can be further enhanced. Please see the Experimental Designs Or Analyses part.
Other Comments Or Suggestions: I didn't observe obvious typos. Authors may consider replace "can not" to "cannot".
Questions For Authors: Can the authors comment on the potential drawbacks of the proposed method or, more generally, using TV divergence, compared to PPO and TRPO, such as instabilities? And will add KL regularization to PPO make it better?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer SqU8,
Thank you for your constructive feedback. Below, we will address your concerns.
>PPO is widely used in large-scale RL problems, and KL regularization will be incorporated when the policy NN is complex, such as LLM...
We appreciate your suggestion. However, the purpose of KL regularization in PPO for LLMs is to prevent reward over-optimization and catastrophic forgetting caused by policy collapse. This does not prevent PPO's ratio deviation issue, as ratio deviation is defined with respect to the initial policy $\pi_ {\theta_ {\mathrm{old}}}$ at each update. Additionally, due to the limited rebuttal period, we may not be able to provide comparative results of SPO-fine-tuned LLMs. We sincerely apologize for this limitation.
>Another interesting ablation will be to decrease PPO's $\epsilon$ or increase SPO's $\epsilon$ so that their average ratio deviation is the same and see if the ratio is the main reason for SPO's better performance.
>An ablation on SPO's $\epsilon$ will help the readers better understand its robustness.
Thank you for your comment. We have supplemented the following experiments:
| Environment | Ant-v4 | Humanoid-v4 | HumanoidStandup-v4 |Walker2d-v4 |
|--------|-----|------|------|------|
| SPO ($\epsilon=0.1$) | $5045.05\pm1005.02$| $4866.81\pm1230.83$| $160103.83\pm11509.79$ |$3737.86\pm903.16$ |
| SPO ($\epsilon=0.2$) | $4760.69\pm849.75$| $4852.76\pm1414.11$| $178853.55\pm43151.81$ |$2944.91\pm1257.06$ |
| SPO ($\epsilon=0.3$) | $4096.41\pm863.53$| $4532.02\pm1319.04$ |$156627.08\pm8519.33$ |$3193.54\pm1148.36$ |
| SPO ($\epsilon=0.4$) | $3594.85\pm857.46$| $4555.34\pm1497.48$ |$165393.59\pm29599.54$ |$2423.38\pm1112.68$ |
| SPO ($\epsilon=0.5$) | $3258.7\pm854.74$| $2516.6\pm1050.51$ |$149689.79\pm16572.68$ |$2187.09\pm989.88$ |
The results demonstrate that over-large $\epsilon$ (0.5) consistently leads to performance degradation, which aligns with the theoretical lower bound.
>The paper [1] also studies replacing the divergence term to TV divergence but is not discussed.
Thank you for pointing out. We will include this in the related work section in our subsequent revisions.
>The related works that use TV divergence or more general divergence are not thoroughly discussed.
We appreciate the suggestion. However, to our knowledge, [2] is the only existing work that discusses the relationship between total variation (TV) divergence and the policy ratio, we have discussed this paper in our related work section. KL divergence is first proposed in original TRPO paper [3]. To the best of our knowledge, beyond TV divergence and KL divergence, there appear to be no published works employing more general divergence measures in this context.
>I didn't observe obvious typos. Authors may consider replace "can not" to "cannot".
Thank you for your thorough review. We will carefully incorporate your suggestions.
>Can the authors comment on the potential drawbacks of the proposed method or, more generally, using TV divergence, compared to PPO and TRPO, such as instabilities? And will add KL regularization to PPO make it better?
In fact, we compared a PPO variant with KL regularization (PPO-Penalty), as shown in Figure 4 of our paper. The results demonstrate that SPO achieves superior performance.
Best,
Authors
---
*Reference:*
[1] X Chu et al. A strong on-policy competitor to PPO.
[2] J Queeney et al. Generalized proximal policy optimization with sample reuse.
[3] J Schulman et al. Trust region policy optimization.
---
Rebuttal Comment 1.1:
Comment: Thank the authors for the response. The rebuttal addressed some of my concerns. However, it is still not clear why PPO+KL does not address the ratio deviation issue, since KL regularization is also added between $\pi$ and the initial policy $\pi_ {\theta_ {\mathrm{old}}}$, similar to how ratio deviation is defined. Reviewer 8JyT also shares similar concerns, but I didn't find satisfying answers in both responses. Besides, the authors said they would compare with [1] in the revision, but didn't state the connections and differences. Other parts of my concerns are addressed.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer SqU8,
Thank you for your additional comments. To address your concerns, as per your request, we have supplemented the performance of PPO+KL, POP3D, and SPO in the MuJoCo environment:
| Algorithm | Ant-v4 | Humanoid-v4 | HumanoidStansup-v4 | Walker2d-v4 |
|--------|-----|------|------|------|
| PPO+KL | $1588.32\pm663.4$| $764.03\pm108.08$| $135953.03\pm26110.9$ | $2563.23\pm912.8$ |
| POP3D | $-490.43\pm674.98$| $349.93\pm158.44$ |$70518.6\pm20164.79$ | $569.14\pm120.94$ |
| SPO | $3900.77\pm1099.6$| $3771.03\pm1461.88$ |$159541.83\pm35398.75$ | $2416.72\pm804.08$ |
For PPO+KL, we employed an adaptive penalty coefficient beta based on the KL divergence. For POP3D, we referred to the hyperparameter settings in [1]. The above results were obtained using a 7-layer network across 4 random seeds. As observed, SPO still achieved the best performance.
Additionally, we found that as the network deepens, POP3D often fails to effectively constrain the probability ratio and KL divergence, leading to suboptimal performance. Moreover, naively applying PPO with KL divergence penalty does not appear to effectively enhance its performance.
Regarding the difference between SPO and POP3D in [1], we believe the most fundamental distinction lies in the fact that SPO imposes a specific penalty coefficient $\frac{|\hat{A}(s_t,a_t)|}{2\epsilon}$ on each data pair $(s_t,a_t)$, whereas POP3D defines a **point probability distance** as a lower bound for the TV divergence.
However, in practice, we can achieve a similar effect by directly constraining the probability ratio, because the probability ratio deviation $|\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}-1|$ with a sufficiently large batch size approximately equals the TV divergence $D_ {\mathrm{TV}}(\pi\Vert\tilde{\pi})$.
Limiting the probability ratio deviation $|\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}-1|$ is more straightforward because the probability ratio also appears in the **surrogate objective** $\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}\cdot\hat{A}(s_t,a_t)$, which naturally leads to
$\max_ {\tilde{\pi}}\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}\cdot\hat{A}(s_t,a_t)$
$\mathrm{s.t.}|\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}-1|\leq\epsilon\Leftrightarrow 1-\epsilon\leq\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}\leq 1+\epsilon$
Using a penalty function, and to ensure convexity and differentiability, a squared penalty can be employed. As a result, we are trying to optimize
$J(\theta)=\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}\cdot\hat{A}(s_t,a_t)-k\cdot(\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}-1)^2=r_t(\theta)\cdot\hat{A}(s_t,a_t)-k\cdot(r_t(\theta)-1)^2$
Based on the previous analysis, we want the probability ratio deviation $|r_t(\theta)-1|$ to be constrained because its expectation is the TV divergence. Therefore, the boundary for the probability ratio is $1+\mathrm{sign}(\hat{A}(s_t,a_t))\cdot\epsilon$.
Note that $J(\theta)$ is a quadratic function of $r_t(\theta)$. Therefore, we want its extremum to lie exactly on the constraint boundary $1+\mathrm{sign}(\hat{A}(s_t,a_t))\cdot\epsilon$, ensuring that the probability ratio deviation $|r_t(\theta)-1|$ will be constrained as long as the number of iterations is sufficient. Then we will find that when $k=\frac{|\hat{A}(s_t,a_t)|}{2\epsilon}$, this condition is exactly satisfied, which ultimately leads to the objective of SPO:
$J(\theta)=\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}\cdot\hat{A}(s_t,a_t)-\frac{|\hat{A}(s_t,a_t)|}{2\epsilon}\cdot(\frac{\tilde{\pi}(a_t|s_t)}{\pi(a_t|s_t)}-1)^2=r_t(\theta)\cdot\hat{A}(s_t,a_t)-\frac{|\hat{A}(s_t,a_t)|}{2\epsilon}\cdot(r_t(\theta)-1)^2.$
For POP3D, its core idea is similar to that of SPO, as both aim to constrain the TV divergence. However, SPO ensures stable probability ratio deviation due to its adaptive penalty coefficients $k=\frac{|\hat{A}(s_t,a_t)|}{2\epsilon}$ and convexity.
We sincerely appreciate your valuable feedback on our paper. As this is our final response, if all your concerns have been addressed, we would also kindly ask for your stronger support for our paper. Thank you!
Best,
Authors
---
*Reference:*
[1] X Chu et al. A strong on-policy competitor to PPO. | null | null | null | null | null | null |
Selective Response Strategies for GenAI | Accept (poster) | Summary: This paper introduces the concept of "selective response" for GenAI systems.
Based on this notion, the contribution of the paper is two-fold.
First, on the conceptual side, it presents a stylized model with two platforms (a GenAI system and a human-driven forum) where users choose between them sequentially. In this model, by sometimes not responding optimally, GenAI systems drive users to human forums like Stack Overflow, generating valuable training data that later improves the GenAI system.
On the technical side, the paper shows that under this model, selective response can improve both GenAI revenue, user welfare, or even both, compared to always-responding. Finally, the work provides an approximately optimal algorithm for maximizing GenAI revenue under social welfare constraints.
Claims And Evidence: The main results of the work are theoretical. In particular, the paper shows that
* Selective response can Pareto-dominate always-responding strategies (Observation 3.1)
* The revenue inefficiency of always responding can be unbounded (Proposition 3.2)
* Selective response can nearly double social welfare in some instances (Proposition 3.3)
* For any strategy, a selective modification generates more future data (Theorem 4.1)
The claims are primarily theoretical, with formal proofs. I have checked the main proof of Theorem 1.1 and 1.2, and the proofs are sound.
At a conceptual level, the insight from this paper challenges the conventional notion that
GenAI should always provide answers. I find that this idea is well supported by the theoretical claims.
(It's not a weakness of the work at all, but note that the paper is not experimental and provides no empirical benchmark to evaluate their results.)
Methods And Evaluation Criteria: The paper uses a game theoretical model to study the dynamics between GenAI and human responses on question-answer platforms. I think the lens of game theory is appropriate for analyzing strategic interactions between platforms and users.
Under this model, the paper provides a theoretical guarantee on selective response and inspired by that, an approximately optimal algorithm for social welfare.
While the theoretical results, in my view, are strong and significant, they are somewhat simplified relative to the real-world GenAI dynamics. For example, as the author(s) admitted, the paper only considers the case where a single GenAI platform exists. Incooporating the full dynamics of multiple GenAI platforms and/or modelling multiple heterogeneous user distributions could make the work stronger.
Theoretical Claims: I reviewed several of the key theoretical claims, mostly surroudning theorem 1.1 and 1.2. The proofs appear sound.
Experimental Designs Or Analyses: The paper is primarily theoretical and does not include empirical experiments. While this is acceptable for a foundational theoretical paper, even simple simulations would have strengthened the work. Specifically, I wonder if the dynamics can be simulated by multiple self-training rounds on synthetic data with simpler models.
Supplementary Material: I have not reviewed the supplementary material.
Relation To Broader Scientific Literature: I am not familiar with the literature on game theory
Essential References Not Discussed: I am not familiar with the literature on game theory
Other Strengths And Weaknesses: Overall, I find the paper very well written and clearly structured.
The conceptual message was delivered and supported by the theoretical claims. Importantly, I think the regulatory perspective provides actionable insights for policymakers (section 6), where they give conditions under which policy interventions improve welfare.
To my knowledge, the main theoretical framework of the paper is novel (though, again, I am not an expert in game-theory or the study of AI and society).
As the author(s) acknowledged, the paper does make a few simplifying assumptions, although, in my view, this is a good work as the first step in studying this dynamics between GenAI and human responses. Finally, I believe the paper could be strengthened if the author(s) could validate their results with a bit of experimental simulation.
Given the strength of the theoretical results and novelty of the main framework, I lean towards accept.
Other Comments Or Suggestions: na
Questions For Authors: Have you considered how users might react if they become aware of selective response strategies from GenAI? Also, do we assume that, when posting contents, the GenAI always reveal their identity, if that matters at all under this model?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the thoughtful evaluation and for finding our work novel.
Addressing the reviewer's questions:
1. Regarding "*how users might react if they become aware of selective response strategies from GenAI?*"
While we model users as non-strategic and indifferent to the actions of GenAI, we totally agree that this might be a concern. There are many ways to reconcile it:
- This behavior is akin to multi-armed bandit settings, in which to maximize the total reward, we sometimes have to explore (trading short-term reward for future rewards). Users that participate in exploration rounds effectively receive a lower utility from the system. We cannot argue that users will comply with this behavior for the GenAI case, but such multi-armed bandit mechanisms are prevalent in real-world settings.
- If selective response is used in a way that is opaque to users, users would not be able to tell. Thus, we can assume they are indifferent to it. Alternatively, if GenAI is transparent about its need for more data on a matter, a message that could be conveyed by saying it has low confidence, users might respond allostratically.
- Future work could explicitly model user dissatisfaction of deliberate selective response, potentially optimizing revenue, welfare, or other metrics under more complex user behavior.
This comment is spot-on, and, upon acceptance, we intend to use the extra space to extend this discussion. Thanks for raising it.
2. Regarding "*do we assume that, when posting contents, the GenAI always reveal their identity, if that matters at all under this model?*" We do not make any assumptions regarding GenAI revealing user identities. Moreover, GenAI's actions are independent of user identities.
The reviewer also mentions that studying "*the full dynamics of multiple GenAI platforms… could make the work stronger.*" Moving from one GenAI to several requires a more game-theoretic approach; we see this as a promising future work. Our intuition is that we would get a Prisoner's Dilemma-like interaction. If one platform chooses to withhold responses, it benefits all other platforms while preserving the same data generation dynamics as always responding. Conversely, if all platforms choose to withhold, they would collectively be better off. In this scenario, the payoffs (expected revenue) depend on the decisions of all platforms as well as user preferences. As in the classic Prisoner's Dilemma, collective cooperation (i.e., not answering) could be enforced through contracts or incentivized by other means.
---
Rebuttal Comment 1.1:
Comment: Thanks for clarifying my questions! I look forward to a future work on multi-platform setting.
I raised my rating and would recommend accept. | Summary: This paper contributes a framework for optimizing model generation for data generation (e.g., encouraging engagement on a forum) and long-term revenue rather than for quality and completeness of response. The authors adopt a two party model where a generative model and a forum share a user set. Over a series of time steps, users decide between GenAI and Forum by comparing the expected utility they derive from each platform. Notably, the GenAI utility is defined by a cumulative data function while the Forum utility is constant. They then show the always-responding condition is Pareto-dominated by selective response, contrasting social welfare and GenAI’s revenue.
The authors' model closely relates to economics papers like Bergemann & Bonatti (2024) and McIntyre & Srinivasan (2017), which consider how platforms & data accumulation, shape user experiences and firm outcomes. To this end, the contributions are specifically a framing of how selectively *not* responding may benefit the overall ecosystem.
Claims And Evidence: 1. This work is a purely theoretical paper with no experimental data, simulations, or case studies to validate the claim that selective response increases data quality or user welfare. The work falls closer to traditional economics than representative learning, but it is topically of great interest to the ICML community.
2. The paper does what it claims, with a number of assumptions that introduce limitations or constraints on its usefulness. For example, the assumption that Forum utility can be treated as a constant is surprising through perhaps reasonable simplification. Forum utility can also be a function of cumulative content or user engagement, which may add complexity to the analysis but benefits the GenAI system (GenAI gets more training data for new content, at a compounding rate)--and can be done without extending into two-player strategic games. The concept of “not responding” is homogenized, but in practice there are substantive differences between refusal, incorrect information, and redirection (sending users to the Forum), each of which would have different effects on user experience, and similarly offer different penalties. These simplifications are largely fine, however, given this is an idealized model.
3. The softmax definition of user choice is symmetric and memoryless (though includes a sensitivity parameter that captures users’ responsiveness to utility differences). It doesn’t account for any of the following effects:
(1) User stickiness (repeated use of the same platform)
(2) Frustration penalty if GenAI gives poor/no answers
(3) Platform trust (e.g., if GenAI’s quality fluctuates, do users downgrade expectations?)
all of which are important context for the argument that GenAI platforms benefit from refusal / incomplete responses. To be more concrete, single-round decisions are a significant simplification.
Methods And Evaluation Criteria: There is no substantive evaluation as this is a theoretical paper.
Theoretical Claims: I read carefully through 4.1. Selective Response Implies Increased User Proportions and Appendix D.1. They are correct, though the proof is parameter-sensitive and assumes exact retraining each round, no delays or stochasticity. Again, as this is intended as simplified model of the setting this is reasonable. I do, however, believe the paper would benefit from further exposition on the limitations of the work.
Experimental Designs Or Analyses: There are none.
Supplementary Material: I read through parts of the supplementary material, specifically D.
Relation To Broader Scientific Literature: This paper offers a novel framing for how GenAI providers might choose to give partial / incomplete / no information in response to key queries, thus incubating discourse and data production on alternative platforms (ensuring additional data is available in the future). The framing is nice, though substantively limited, and as a first step offers several directions for future work to build upon.
Essential References Not Discussed: The related works are largely covered within the paper. The authors may be interested in extended discussion contrasting generated data with human-produced data, such as Shumailov et al. (2023), “The Curse of Recursion: Training on Generated Data Makes Models Forget" as further motivation for emphasizing human data production.
Other Strengths And Weaknesses: The setting is novel and of interest to the community. The paper is generally well-written. There are a number of assumptions that introduce some weaknesses to the work. More substantively, given the ICML setting, there are no simulations or other forms of evaluation to show the model holds in practice.
Other Comments Or Suggestions: The regulator's capabilities are barely sketched. It would be nice to include further discussion on this point by the authors.
*** I have updated my score to reflect the authors continued rebuttal engagement and addition of simulation.
Questions For Authors: See above!
Code Of Conduct: Affirmed.
Overall Recommendation: 5 | Rebuttal 1:
Rebuttal: We thank the reviewer for the useful feedback and for finding our work novel.
We find the works you mentioned, namely Bergemann & Bonatti (2024), McIntyre & Srinivasan (2017), and Shumailov et al. (2023), highly relevant and will incorporate them into our literature review. Thank you for pointing us to them.
Regarding the "*assumptions that introduce some weaknesses to the work*", we fully agree with the reviewer's observation. Our goal was to present a simplified and clean model to highlight the conceptual benefits of using selective responses. While our assumptions impose certain limitations on our results, we have carefully ensured that each assumption is well-motivated. Additionally, we believe that some assumptions could be relaxed while preserving the conceptual contribution, though this will come at the cost of less clean results. We thank the reviewer for bringing this up, as we believe that addressing this point would be a great addition to our paper.
The reviewer mentioned that "*The softmax definition of user choice is symmetric and memoryless… It doesn't account for any of the following effects: (1) User stickiness (2) Frustration penalty if GenAI gives poor/no answers (3) Platform trust*". The reviewer is correct in pointing this out as an aspect we do not address. Capturing all possible factors in a single model is challenging and often makes theoretical analysis impossible. Therefore, these aspects are fascinating research directions that offer opportunities for new stylized theoretical frameworks as well as comprehensive empirical work.
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Rebuttal Comment 1.1:
Comment: As long as the authors expand their discussion on limitations (and thus for future work) I will leave my score as it stands.
I do think the addition of some form of simulation would strengthen the work given the setting, but leave it to the authors to do as they please. If they agree to add something along these lines I will update my score to the highest accept ✨
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Reply to Comment 1.1.1:
Comment: We appreciate the reviewer's quick reply.
As the reviewer suggested, we intend to expand the discussion on limitations and future work.
Additionally, we have carefully considered the reviewer’s suggestion regarding simulations. We tried to identify a form of simulation that "*would strengthen the work given the setting*," which turned out to be a challenging task. After discussion and brainstorming, we believe we have found a way to provide additional insights into the model using simulations, insights that would be difficult to derive formally.
Below, we outline the simulations we intend to add to the paper. Importantly, ***we consider this to be a very minor change.*** The total runtime is under an hour on a standard laptop, and the corresponding write-up will take just few hours. We can either put this part in the appendix or use the extra page, so no editing is needed. We mention this to reassure the reviewer (and area chair) that this is not a major revision and certainly not an entirely new submission.
The simulations analyze how profitable it is for GenAI to deviate from the full response strategy, providing a sensitivity analysis of the following parameters:
1. The discount factor $\gamma$.
2. The power $\alpha$, where we model the revenue as $r(p)= p^\alpha$.
Intuitively, selective response becomes superior with greater values of $\gamma$ and $\alpha$. The reasoning is simple: A low discount factor implies a strong preference for the present over the future, making it suboptimal to "waste" present users by not responding. Similarly, a high power $\alpha$ implies that sacrificing present users can result in superlinear revenue gains in the future, making selective response more attractive.
We use our ASR algorithm to test these intuitions, as well as a staircase heuristic for instances where Assumption 2.1 does not hold. Since both methods are suboptimal, any revenue improvement over the full response strategy implies that the optimal policy would achieve even higher gains.
Our simulations fully support this intuition.
We believe these simulations will strengthen the paper, and we are grateful to the reviewer for encouraging this addition. Thank you! | Summary: In this paper, the authors introduce a selective response model where a "GenAI system" behaves strategically -- e.g, giving lower quality response, does not respond, etc. They provide a game theoretic based proof that shows that selective response can be beneficial in practice, when the other option is to utilize a human-based forum.
Claims And Evidence: Claims are well-supported by evidence
Methods And Evaluation Criteria: The work is primarily theoretical
Theoretical Claims: Mathematical proofs were not thoroughly checked
Experimental Designs Or Analyses: - The game theoretical model makes sense, though it debatable how ethical some choices (e.g., providing partial knowledge etc.) is meaningful. Under this case, the two actions that GenAI can take seem limited (either generate or defer).
- The utility of such an approach in a real-world setting (via simulation) would have improved the paper, and clarified the findings
Supplementary Material: - Supplementary materials were not reviewed in detail
Relation To Broader Scientific Literature: - The work relates to optimal policies that GenAI should adopt, assume a multi-competition market
- The work is also related to algorithmic deferral [1], which the authors have not considered explicitly in the related work section
References:
[1] Hemmer, Patrick, et al. "Learning to defer with limited expert predictions." Proceedings of the AAAI Conference on Artificial Intelligence. Vol. 37. No. 5. 2023.
Essential References Not Discussed: - The authors could connect their work to the selective prediction / deferral literature (though their model is different from standard prediction-based tasks studied in prior works) -- for example, [1,2]
[1] Hemmer, Patrick, et al. "Learning to defer with limited expert predictions." Proceedings of the AAAI Conference on Artificial Intelligence. Vol. 37. No. 5. 2023.
[2] Mozannar, Hussein, and David Sontag. "Consistent estimators for learning to defer to an expert." International conference on machine learning. PMLR, 2020.
Other Strengths And Weaknesses: - Work addresses a meaningful gap in literature, and clearly elucidates limitations (e.g. assumption of single algorithmic competitor, non-strategic forum behavior, etc.)
- However, the scope of such selective response strategies in the real world could be considered more closely -- for example, is actively withholding knowledge possible?
Other Comments Or Suggestions: - Can authors expand on how models would scale to multiple GenAI agents?
Questions For Authors: - Can authors expand on how models would scale to multiple GenAI agents?
- Do some of the selective actions -- for example, actively withholding knowledge -- seem feasible in the real world? That is, do we expect value in any action except choosing not to produce an output vs producing an output?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's positive and helpful feedback, we hope to leverage it to improve our paper.
Indeed, our work "*is also related to algorithmic deferral.*" We thank the reviewer for making this connection, which we weren't aware of. We shall address the two papers in our related work.
The reviewer mentions that "*the scope of such selective response strategies in the real world could be considered more closely,*" asking whether "*actively withholding knowledge possible.*"
We believe that selective responses are indeed feasible. To exemplify, recommender systems often face exploration-exploitation tradeoffs, where taking a risky action today (uncertain whether the user will like it or not) trades present rewards with future gains. In this example, the system "selectively" chooses the non-myopic option (sub-optimal in the present) to gain information to improve its utility in the future. In our paper, GenAI prefers inaccurate answers and (slightly) unsatisfied present users with more accurate answers and satisfied future users.
Does this make sense? We came up with this argument while discussing your review. If you find it convincing, we can elaborate on it and include it in the paper.
Answering your specific questions,
1. Regarding extending on "*how models would scale to multiple GenAI agents.*" Multiple GenAI platforms could induce a Prisoner's Dilemma-like interaction. If one platform chooses to withhold responses, it benefits all other platforms while preserving the same data generation dynamics as always responding. Conversely, if all platforms choose to withhold, they would collectively be better off. In this scenario, the payoffs (expected revenue) depend on the decisions of all platforms as well as user preferences. As in the classic Prisoner's Dilemma, collective cooperation (i.e., not answering) could be enforced through contracts or incentivized by other means. This is a fascinating research direction, and we intend to expand on it in our discussion. Thanks for bringing this up.
2. Regarding "*do we expect value in any action except choosing not to produce an output vs producing an output?*" Just to be sure: Does the reviewer mean answering with varying quality? That is, could it provide lower-quality answers than GenAI could produce deliberately? If that is the case, from a theoretical perspective and for our purposes, there is no substantial difference between providing low-quality answers to all users or providing the highest-quality answers to a subset of users. All the theoretical results extend to lower-quality answers as well. Selective response serves as the mechanism for controlling whether GenAI invests its full efforts with the hope of driving users to generate more data.
---
Rebuttal Comment 1.1:
Comment: Thanks to the authors for responding! Regarding 2. the question was about the real world implications of withholding knowledge, even when it could have been answered. That is, is actively withholding knowledge an ethical response? I think your response partially addresses this already
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Reply to Comment 1.1.1:
Comment: Thank you for your comment.
One way to think about withholding information (or responding with lower-than-possible quality) is as a means to trade off the utility of current users with the utility of future users. This principle lies at the heart of online algorithms---balancing exploration and exploitation.
To make this more concrete, consider the Upper Confidence Bound (UCB) algorithm or Thompson Sampling. These algorithms occasionally choose actions (arms) not because they are currently optimal but because they have not been sufficiently explored. As a result, some users receive suboptimal outcomes purely to improve the system's future performance. This is analogous to the case we discuss, where certain users may receive lower-quality answers to improve the quality of information available to future users.
It's worth noting that one of the original motivations for multi-armed bandits came from medical treatment allocation [1]. Thompson's seminal paper [2], published in Biometrika, laid the foundation for adaptive clinical trials---clearly a domain involving high-risk, high-reward scenarios where such exploration-exploitation tradeoffs are not only present but critical.
Once again, we emphasize our belief that such actions must be transparent. Specifically, users should be notified that the system employs such a strategy and informed that this is done to improve overall social welfare. | Summary: The paper introduces a novel strategy called "selective response" for Generative AI (GenAI) systems, particularly in the context of human-based forums like Stack Overflow. The main idea is that GenAI could strategically provide inaccurate or conservative responses to queries involving emerging topics and novel technologies, thereby driving users to use human-based forums. This approach aims to create a compounding effect on the data generation process, ultimately increasing both GenAI's revenue and user welfare in the long term. The paper presents a game-theoretic model to explore the dynamics of content creation, welfare, and revenue. Key contributions include:
- Conceptual Contribution: The paper is the first to explore selective response for GenAI, proposing a model where GenAI strategically chooses when, if, and how to engage with user queries.
- Technical Contribution: The authors demonstrate that selective response can Pareto-dominate the always-responding approach, improving user welfare and GenAI's revenue. They also provide an approximately optimal algorithm for maximizing GenAI's revenue under social welfare constraints.
- Regulatory Perspective: The paper derives sufficient and necessary conditions for selective response to improve welfare improvements, offering insights for regulators.
Claims And Evidence: The claims made in the paper are generally supported by clear and convincing evidence. The authors provide a detailed game-theoretic model and derive theoretical results that support their claims. For example, Theorem 1.1 and Theorem 1.2 are supported by rigorous proofs and examples. The paper also includes a discussion on the long-term effects of selective response, supported by Theorem 4.1 and Theorem 4.4. However, some claims, particularly those related to the practical implementation of selective response, could benefit from more empirical validation.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria are appropriate for the problem at hand. The game-theoretic model is well-suited to analyze the strategic interactions between GenAI and human-based forums. The authors use a sequential setting over discrete rounds, which allows them to explore the dynamics of content creation, welfare, and revenue. The evaluation criteria, such as the accuracy function and the utility functions, are well-defined and align with the objectives of the study.
Theoretical Claims: The theoretical claims in the paper are supported by detailed proofs. For example, Theorem 4.1 is supported by a proof sketch that demonstrates the compounding effect of selective response. Theorem 4.4 is supported by an approximately optimal algorithm (ASR) and its analysis. The proofs are generally clear and convincing, though some technical details are deferred to the appendix, which is common in theoretical papers.
Experimental Designs Or Analyses: The paper is primarily theoretical, and as such, it does not include experimental designs or analyses. However, the theoretical analyses are sound and well-justified. The authors provide examples and simulations to illustrate their findings, which help to validate the theoretical results.
Supplementary Material: The supplementary material includes additional proofs and technical details that support the main claims of the paper. For example, the appendix contains proofs for propositions and lemmas that are referenced in the main text. The supplementary material is well-organized and provides additional clarity on the theoretical results.
Relation To Broader Scientific Literature: The paper is well-situated within the broader scientific literature on generative AI and game theory. It connects to emerging research on foundation models, competition between generative AI and human content creators, and the impact of generative AI on content diversity. The authors also draw on economic literature on information design and signaling, which adds depth to their analysis. The paper builds on prior work by introducing a novel approach (selective response) and demonstrating its potential benefits.
Essential References Not Discussed: The paper does a good job of citing relevant literature, but it could benefit from discussing more recent work on the interaction between AI systems and human content creation platforms. For example, recent studies on the impact of AI on user behavior and data generation in online forums could provide additional context for the proposed selective response strategy.
Other Strengths And Weaknesses: Strengths:
- The paper introduces a novel and creative approach (selective response) that has the potential to significantly impact the development of GenAI systems.
- The theoretical analysis is rigorous and well-supported by proofs and examples.
- The paper provides valuable insights for both GenAI companies and regulators, making it relevant to both academic and industry audiences.
Weaknesses:
- The paper is primarily theoretical, and the practical implementation of selective response is not explored in depth. Empirical validation would strengthen the paper's claims.
- The model assumes a single GenAI platform, which may not fully capture the complexities of real-world scenarios with multiple competing platforms.
Other Comments Or Suggestions: The paper is well-written and clearly presents its contributions. However, it could benefit from a more detailed discussion of the limitations and potential challenges of implementing selective response in practice. Additionally, the authors could consider exploring the ethical implications of selectively withholding information from users.
Questions For Authors: - Question 1: How do you envision the practical implementation of selective response in real-world GenAI systems? What are the potential challenges and how might they be addressed?
Response Impact: A detailed discussion on practical implementation would provide more confidence in the feasibility of the proposed strategy.
- Question 2: Have you considered the ethical implications of selectively withholding information from users? How might this impact user trust and satisfaction?
Response Impact: Addressing ethical concerns would strengthen the paper's relevance and appeal to a broader audience.
- Question 3: Could you elaborate on how the model might be extended to account for multiple competing GenAI platforms?
Response Impact: Extending the model to multiple platforms would make the analysis more robust and applicable to real-world scenarios.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We appreciate the reviewer's thoughtful and positive evaluation of our work.
Regarding "*The paper does a good job of citing relevant literature, but it could benefit from discussing more recent work on the interaction between AI systems and human content creation platforms*". Given your advice, we have discovered [1-3] below, which we intend to address in the paper. If you have additional pointers to relevant work, we would appreciate it.
Addressing the reviewer's specific questions and concerns,
1. Regarding "*How do you envision the practical implementation of selective response in real-world GenAI systems?*" Platforms like Stack Overflow, providing both GenAI services [4] and user-driven forums, could implement selective response mechanisms. In the broader GenAI market, companies may need to establish contractual agreements governing the use of selective responses. For example, platforms could selectively respond to queries about emerging topics by withholding answers when the LLM of all major companies' confidence falls below a predefined threshold. Given your question, we shall elaborate on this aspect in the paper.
2. Regarding "*Have you considered the ethical implications of selectively withholding information from users? How might this impact user trust and satisfaction?*" Choosing not to answer may be beneficial when GenAI is uncertain about the correctness of its response (or if the response is not sufficiently accurate). In such cases, users may appreciate transparency if they are informed in advance that the expected answer quality is low. We do acknowledge that aggressive selective response could lead to an undesired behavior if this transparency is perceived as unreliability. Indeed, our work suggests opportunities and freedom to apply selective response strategies to real-world systems. We shall address this in our discussion.
3. The reviewer asks, "*Could you elaborate on how the model might be extended to account for multiple competing GenAI platforms?*" Multiple GenAI platforms could induce a Prisoner's Dilemma-like interaction. If one platform chooses to withhold responses, it benefits all other platforms while preserving the same data generation dynamics as always responding. Conversely, if all platforms choose to withhold, they would collectively be better off. In this scenario, the payoffs (expected revenue) depend on the decisions of all platforms as well as user preferences. As in the classic Prisoner's Dilemma, collective cooperation (i.e., not answering) could be enforced through contracts or incentivized by other means. This is a fascinating research direction, and we intend to expand on it in our discussion, thanks for bringing this up.
References:
[1] R Maria del Rio-Chanona, Nadzeya Laurentsyeva, Johannes Wachs, Large language models reduce public knowledge sharing on online Q&A platforms.
[2] Gordon Burtch, Dokyun Lee, Zhichen Chen, The consequences of generative AI for online knowledge communities.
[3] Xinyu Li, Keongtae Kim, Impacts of generative AI on user contributions: evidence from a coding Q&A platform.
[4] https://stackoverflow.blog/2023/07/27/announcing-overflowai/ | null | null | null | null | null | null |
Deep Linear Network Training Dynamics from Random Initialization: Data, Width, Depth, and Hyperparameter Transfer | Accept (poster) | Summary: This work provides a theoretical analysis of gradient descent dynamics in deep linear networks trained at large widths from random initialisation. Specifically, gradient descent dynamics, hyper-parameter transfer effects and asymptotic descriptions for deep networks were analysed and discussed.
Claims And Evidence: Claims are backed by rigorous theoretical derivations.
Methods And Evaluation Criteria: The evaluation is purely theoretical and does not include standard deep learning benchmarks.
Theoretical Claims: Mathematical formulations are elegant but not carefully verified.
Experimental Designs Or Analyses: Experimental experiments are relatively limited.
Supplementary Material: No supplementary material available.
Relation To Broader Scientific Literature: Insights on width-depth interactions and hyper-parameter transfer are quite novel, but focusing linear networks limits its scope and application in real cases.
Essential References Not Discussed: Not applicable.
Other Strengths And Weaknesses: The paper provides strong theoretical insights, but lacks extensive empirical validation on real-world datasets.
Other Comments Or Suggestions: None.
Questions For Authors: No specific questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank the reviewer for appreciating our theoretical contributions and the novelty of attempting to capture the hyperparameter transfer effect.
### Methods and Evaluation Criteria
*The evaluation is purely theoretical and does not include standard deep learning benchmarks.*
The purpose of this paper is primarily theoretical and focuses on a linear networks, rather than an experimental paper purporting to perform well on benchmarks.
### Theoretical Claims
*Mathematical formulations are elegant but not carefully verified.*
We provide a derivation of our results in the Appendix using techniques from statistical mechanics. We also verify our equations under the conditions of our theory (randomly initialized deep linear networks trained on random data) using simulations.
### Relation To Broader Scientific Literature:
*Insights on width-depth interactions and hyper-parameter transfer are quite novel, but focusing linear networks limits its scope and application in real cases.*
Our focus on linear networks was motivated by finding the **simplest possible model** that exhibits the phenomenon of interest (which in this case is the learning rate transfer effect).
### Other Strengths And Weaknesses
*The paper provides strong theoretical insights, but lacks extensive empirical validation on real-world datasets.*
Since we are focused on the dynamics of **linear networks**, the generalization on most real-world datasets would not be very good. However, we can attempt to include an experiment on a simple task like MNIST, which due to its power law covariance spectrum (see Figure 6a here https://arxiv.org/abs/2409.17858) would likely look similar to our Figure 6c. | Summary: This work theoritically characterizes the gradient descent dynamics in deep linear networks in the asymptotic limit of infinite data and width of the network. They study the limiting behaviour of both deep linear network and residual deep network for both isotropic data and data with power-law covariance and studies the effect of depth, richness, batch-size and hyper-parameter transfer.
Claims And Evidence: Yes, the claims and evidence are convincing. However, some parameters remains undefined, so it is difficult for the reader to grasp the essence of the results.
Methods And Evaluation Criteria: It is mostly linear networks and labels genrated by linear models.
Theoretical Claims: The proofs and the theory looks mostly correct to me except some minor questions:
1) $\gamma_{0}$ is defined nowhere in the text and it is hard to grasp the meaning of this quanitity alhtough i see several results depend on it.
2) In equation-10, no effect of learning rate or intializations scale is captured. It is well known that rich regime is mostly captured with small initialization and small learning rate, but this result was not seen from the theory result.
3) Linear networks are known to exhibit saddle to saddle behaviour (for rich dynamics)...However, is it true that this dynamics can't be captured by isotropic random data?
Experimental Designs Or Analyses: Yes, they are valid.
Supplementary Material: Yes, i glanced through the proofs. They seemed correct.
Relation To Broader Scientific Literature: Studying the dynamics of deep linear networks is an important first step to understand deep neural networks. This work should be highly relevant.
Essential References Not Discussed: Although there are tons of works on deep linear networks, I think the current refernces are sufficient for the paper.
Other Strengths And Weaknesses: 4) The effect of learning rate seemed to be missing from the result. What about the alignment between singular vector for each layer? Does the traditional result of implicit bias of gradient flow and descent captureed here? It seemed no from the current result. Discussing this in details would be more useful.
Other Comments Or Suggestions: 1) Please define $\mu P$.
2) In section-2.1, dynamics are studies in the aymptotic limit of P,D,N. However, why is there a further limit on $\alpha$ and $\alpha_{B}$. This imit was unclear.
## update after rebuttal
I have read the rebuttal and decided to stick with my score of weak accept.
Questions For Authors: Please answer points 1,2,3,4.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their careful reading and detailed comments and questions. We address the main concerns below.
### Theoretical Claims
*$\gamma_0$ is defined nowhere in the text and it is hard to grasp the meaning of this quantity alhtough i see several results depend on it.*
We will define this hyperparameter more clearly. Mechanically it is present in the definition of the predictor $f = \frac{1}{\gamma_0} w^L ... W^0 x$. This scalar basically controls the laziness/richness of the learning dynamics with $\gamma_0 \to 0$ giving the lazy (kernel) regime. For $\gamma_0 \gg 0$, the dynamics are far from the kernel regime. We have added more explanation of this and also shown that $\gamma_0 \to 0$ limit gives the kernel regime. The dependence of $\gamma_0$ on network width also defines the difference between NTK parameterization and mean-field/$\mu$P scaling.
*In equation-10, no effect of learning rate or intializations scale is captured. It is well known that rich regime is mostly captured with small initialization and small learning rate, but this result was not seen from the theory result.*
Equation 10 depends implicitly on the hyperparameter $\gamma_0$ which we are using to control the laziness/richness. We can alternatively manipulate the initail variance of the weight entries which would have a similar effect.
*Linear networks are known to exhibit saddle to saddle behaviour (for rich dynamics)...However, is it true that this dynamics can't be captured by isotropic random data?*
Our dynamics would start at a *single saddle point* for $\gamma_0 \gg 1$ limit with the learning rate scaled down. We could induce **multiple saddles** (saddle-to-saddle behaviors) in a multiple output channel setting with isotropic features, especially if we also allow for small initial weights. We have equations for this setting (Appendix G) but have not numerically integrated them yet. Indeed, in the small initialization regime this is exactly the setting of the work of Saxe et al 2014 https://arxiv.org/abs/1312.6120.
*The effect of learning rate seemed to be missing from the result. What about the alignment between singular vector for each layer? Does the traditional result of implicit bias of gradient flow and descent captureed here? It seemed no from the current result. Discussing this in details would be more useful.*
Our theoretical equations depend directly on the learning rate such as in equation 11 and equation 67.
Our theory, since it applies to non-negligible random initialization, does not demand perfect alignment between adjacent weight matrices. However, in the rich regime, the alignment does tend to increase. Equation 25 reveals that
$$W^\ell(t) = W^\ell(0) + \frac{\eta\gamma_0}{\sqrt N}\sum_{t'<t} g^{\ell+1}(t') h^\ell(t')^\top$$
The first term is random and static, while the second term improves alignment of $W^\ell$'s left singular vectors with the $\{ g^\ell(t) \}$ vectors which are
\begin{align}
g^{\ell}(t) = \left[ \frac{1}{\sqrt{N}} W^{\ell}(t) \right]^\top ... w^L(t)
\end{align}
If the random initialization were negligible compared to the second term, then all weights would align and become low rank, consistent with prior works. However, our theory can flexibly handle large random initialization in either lazy or rich regimes (for arbitrary values of $\gamma_0$).
### Other Comments or Suggestions
*Please define $\mu$P*
We have added a definition of $\mu$P as "maximum update parameterization", a term introduced in https://arxiv.org/abs/2011.14522. We will add this definition.
*In section-2.1, dynamics are studies in the aymptotic limit of P,D,N. However, why is there a further limit on $\alpha$ and $\alpha_B$. This limit was unclear.*
We apologize that our exposition in this section was unclear to the reader. We will try explaining it more clearly in section 2.1. We basically analyze two settings
1. Full batch gradient descent with a fixed random dataset of size $P$ in a proportional scaling regime $P,D,N\to\infty$ with fixed ratios $P/D = \alpha$ and $N/D = \nu$.
2. Online stochastic gradient descent where at each step a batch of size $B$ is sampled and used to estimate the gradient. We look at $B,N,D \to \infty$ with fixed ratios $B/D = \alpha_B$ and $N/D = \nu$.
We contrast these two settings in Figure 3, where Figure 3 (a,b) is in the first setting and Figure 3 (c,d) is in the second setting. | Summary: This paper develops a DMFT based theory for deep linear networks (with and without residual connections) in GD and SGD settings. The authors show that the theory captures the effect of initialization, dataset correlations, width and depth. Moreover, they show hyperparameter transfer with width and depth.
Claims And Evidence: Yes. The claims made in the paper are supported by evidence. Specifically, the figures validate the theory.
Methods And Evaluation Criteria: Yes. The methods and evaluation make sense.
Theoretical Claims: Yes. I have verified all the theoretical details in the main text and Appendix A, while skimming the remaining Appendices for soundness.
Experimental Designs Or Analyses: Yes. The experimental designs are sound.
Supplementary Material: I have done a sanity check of the Supplementary material. However, it is possible that I might have missed out on details.
Relation To Broader Scientific Literature: This work adds to the ongoing research on understanding the neural networks by focusing on deep linear networks (with residual connections). The work provides insights into the effect of data complexity, width, depth, and random initialization.
Essential References Not Discussed: The essential references are discussed.
Other Strengths And Weaknesses: Strengths
* The paper is clearly written and is easy to follow
* The insights on the complexity of data, depth and width are insightful
Weaknesses
* To the best of my knowledge, the hyperparameter transfer results are known in prior literature in much more complex settings.
* While the Section 3 results are clearly discussed in the Appendix, I found the details for Section 4 and 5 to be sparse in the Appendix. In Appendix C, the authors mention: "After these response functions have been solved for, we must solve for the correlation functions using the single site densities. This gives a closed form prediction for the loss dynamics." but do not provide details. Similarly, it would be helpful to expand on Appendix E details on structured data.
Other Comments Or Suggestions: Comments:
* There is a typo in Equation 9, it should be $W^0$ and not $W^1$.
* Reference for Appendix is missing on line 150.
Suggestions:
* It would be helpful to provide further details for Sections 4 and 5 in the Appendix.
Questions For Authors: Questions:
* Can the authors clarify if they have any additional insights into hyperparameter transfer compared to prior works?
* Do the authors understand why does the loss increase initially in Figure 3 (c, d)?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We thank the reviewer for their careful reading and their support. Below we address the weaknesses.
### Weaknesses
**hyperparameter transfer results are known in prior literature in much more complex settings**
While there are already several cases where hyperparameter transfer are documented (including in complicated architectures like transformers), we were seeking the simplest possible setting which could be theoretically analyzed. To capture hyperparameter transfer effects one needs a setting where (1) model can exit the kernel regime and (2) wider models perform better. The simplest model we could identify with these properties was **randomly initialized deep linear networks**.
**Appendix Explanations Sparse**
We thank the reviewer for this comment. We have made the Appendix sections more detailed and provide the closed form set of equations for the correlation and response functions from the single-site equations. The train and test losses can be computed from the correlation functions $C_v$ and $C_\Delta$.
### Other comments
Thank you for finding these typos and missing links. We have fixed these.
*It would be helpful to provide further details for Sections 4 and 5 in the Appendix.*
We have included additional details to derive the main results of section 4 and 5.
### Questions
*Can the authors clarify if they have any additional insights into hyperparameter transfer compared to prior works?*
Our main result for hyperparameter transfer is that in $\mu$P scaling, the finite width effects accumulate as a combination of effective noise and bias in the dynamics from finite $\nu = N/D$ while the feature updates are approximately independent of $\nu$ (see equation 14).
*Do the authors understand why does the loss increase initially in Figure 3 (c, d)?*
Good question! This initial loss increase is driven by the variance in the predictor from SGD noise (small $\alpha_B$) and small width (small $\nu$). This can be seen from an analysis of the early portion of the DMFT equations where, for the first few steps of training the test loss can be approximated as
$$\mathcal L(t+1) \approx \left[(1-\eta)^2 + \frac{\eta^2}{\alpha_B} + \frac{\eta^2}{\nu} \right] \mathcal{L}(t)$$
The loss will exponentially increase at early times provided that
\begin{align}
\eta > \frac{2}{1+\frac{1}{\alpha_B} + \frac{1}{\nu}} .
\end{align}
Indeed from the simulations we see that for sufficiently large $\alpha_B$ and $\nu$ this initial increase disappears.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the clarifications. I will keep my score. | Summary: The authors analyze several models of deep linear networks (FCNs, ResNets) trained on Gaussian (iid, and power-law covariance) data with noisy Gradient Descent, focusing on hyperparameter transfer between small and large models. They develop a DMFT formulation of the problem which can accommodate finite width, finite learning effects, and dataset average. This results in a series of non-linear saddle point equations on kernels and gradient kernels which are solved numerically. The numerical solutions agree well with simulations of actual neural networks. At least in muP scaling, they argue that the optimal learning rate transfers properly across widths while the loss changes.
Claims And Evidence: I found several issues with the manuscript.
The papers claim to give a theoretical result. However, since theoretical results are delivered implicitly via high-dimensional non-linear equations that require a numerical solver, it is not clear what new understanding one has gained.
A second issue is that optimal learning rate does in fact shift in their setting even in muP. The shift in optimal value itself seems somewhat larger than in Ref. https://arxiv.org/pdf/2203.03466 however the sharpness of the loss makes it so that, in figure 2b, choosing the learning rate based on v=0.5 and transferring to v=5, would incur an order of magnitude change to the loss compared to its optimal value.
A third issue is the concentration of the kernel in NTK scaling. While the authors arrive at an action which has D in front of an seemingly $D$ independent action for the kernels, the orders parameters involved have data indices and hence scale with D. In such circumstances, the saddle point is not clearly justified. A simple example is the Wishart Distribution, wherein by normalizing such that the matrix elements average to the identity, one has a similar structure of probability. However, taking a saddle point would yield a delta function distribution of eigenvalues, whereas in fact the width of the eigenvalue distribution is similar to its average. In muP scaling this issue should go away.
Methods And Evaluation Criteria: See above.
Theoretical Claims: I looked at the derivation, but did not rederive it. I raised above some concerns about the correctness of the saddle point equations in the NTK setting.
Minor comment. Eq. 60 61 are missing summand indices.
Experimental Designs Or Analyses: The experiments look sufficient, apart from the previous comment about the sharpness of the loss.
Supplementary Material: I looked at the derivation at large and apart from the above issue with the saddle point did not find any major issues.
Relation To Broader Scientific Literature: The literature review is Ok.
Essential References Not Discussed: Nothing essential.
Other Strengths And Weaknesses: Strengths:
1. The authors develop a DMFT formalism for deep learning networks which accounts for data-averaging and finite learning rate effects.
2. Although not entirely clear from the manuscript, which doesn't give away absolute scales of D, they seem to push the numerical envelope of solving DMFT equation further.
3. The author provides a toy setting which, despite being too complicated to being solved analytically at the moment, may serves as a stepping stone to future analytical research in this important subfield.
Weaknesses:
1. Presentation: The papers claim to give a theoretical result. However, since the theoretical results are delivered implicitly via high-dimensional non-linear equations that require a numerical solver, it is not clear what new understanding one has gained.
2. Deficiencies of the toy setting: A second issue is that the optimal learning rate does in fact shift in their setting even in muP. The shift in optimal value itself seems somewhat larger than in Ref. https://arxiv.org/pdf/2203.03466 however the sharpness of the loss makes it so that, in figure 2b, choosing the learning rate based on v=0.5 and transferring to v=5, would incur an order of magnitude change to the loss compared to its optimal value.
3. Correctness of derivation for NTK scaling. While the authors arrive at an action which has D in front of an seemingly $D$ independent action for the kernels, the orders parameters involved have data indices and hence scale with D. In such circumstances, the saddle point is not clearly justified. A simple example is the Wishart Distribution, wherein by normalizing such that the matrix elements average to the identity, one has a similar structure of probability. However, taking a saddle point would yield a delta function distribution of eigenvalues, whereas in fact the width of the eigenvalue distribution is similar to its average. In muP scaling this issue should go away.
More minor
4. Some experimental data missing (what is the input dimension in the transfer figures)
5. Does the computational cost for saddle point solvers and networks factor in the ability to parallelize networks? If not, this should be clearly stated.
Other Comments Or Suggestions: No.
Questions For Authors: See previous comments.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for their careful reading and thoughtful questions. Below we address the key questions and concerns and hope that the reviewer will be satisfied with our answers and consider an increase in their score.
**Result Delivered as Complex Nonlinear Equations**
The theoretical results, while still complicated, are **lower dimensional** than the system that we started with. In general, we went from gradient flow dynamics on $(L-1)N^2 + ND + N$ parameters to a system of equations for $4L+4$ correlation/response functions. Compared to other mean field results which involve *non-Gaussian Monte-carlo averages*, this theory is much simpler since all equations for the order parameters close directly.
That said, the critique that **mean field descriptions can be pretty complicated** (especially for nonlinear dynamics) is a valid concern. However, we were able to extract some useful insights from the equations including
1. The divergence of response functions with respect to depth $L$ unless the residual branch is scaled as $1/\sqrt{L}$
2. Approximate scalings of maximum stable learning rate for mean field and NTK parameterizations (see Figure 7).
3. The effect of feature learning on power law convergence rates for power law data (see Figure 6).
4. The DMFT equations generally reveal a **buildup** of finite width (finite $\nu$) and finite data (finite $\alpha$) effects over time. Thus the early part of training is much closer to the "clean limit" where $\alpha,\nu \to \infty$ but later in training there are more significant deviations across model sizes or dataset sizes.
We will mention some of the insights that we can extract from the theory more concretely in the main text and Appendex sections.
**Shift in Optimal LRs**
It is true that learning rate transfer for SGD is not perfect in our model, especially when going from **very small widths** to **very large widths**, we point out a few things
1. The transfer in $\mu$P is much better than for NTK scaling, especially at large widths.
2. The success or failure of transfer is captured by our theory (dashed lines of Figure 2).
3. In realistic $\mu$P experiments other architectural details that are not included in our model (like Layernorm or Adam) improve the hyperparameter transfer effect in $\mu$P. SGD without layernorm in deep nonlinear networks with $\mu$P looks similar to the "sharp" cutoffs we see in our linear network experiments (see Figure 1 (a)-(b) compared to Figure 2b here https://arxiv.org/abs/2309.16620).
**Is the Saddle Point Valid? Do all Eigenvalues Collapse to a Dirac Distribution?**
This is a great question and we thank the reviewer for letting us clear this up! TLDR: Yes, the saddle point is valid and no our equations do not indicate a collapse in the density of eigenvalues, but rather capture Marchenko-Pastur like spread in time-constants.
More detail:
1. We stress that our action is completely independent of $D$ since **none of our vectors of interest carry data indices**. There are only two vectors for each layer $\mathbf h^\ell(t), \mathbf g^\ell(t)\in\mathbb{R}^N$ defined in equation 5. This is the secret sauce of the linear network setting which enables us to take an **exact proportional limit** (note equations 5 and 6 are special for linear networks). Thus the order parameters of interest $C_h^\ell(t,t') = \frac{1}{N} \mathbf h^\ell(t) \cdot \mathbf h^\ell(t')$, etc, also **do not carry data indices**. Thus the number of order parameters is $\mathcal{O}_D(1)$ and we are justified to take the saddle point. This is different than the saddle point of prior works (https://arxiv.org/abs/2205.09653, https://arxiv.org/abs/2304.03408) where the action depends on a number of order parameters which grows with $P$. This is why those works were restricted to $N \to \infty$ limits with $P$ fixed. **We do not take a saddle point over full $P\times P$ matrices but over correlation and response functions.**
2. To illustrate that we are really capturing the full eigenvalue density etc, we can show that our equations for $R_\Delta(t,t')$ can recover the **Marchenko-Pastur law** for a Wishart in the lazy training regime.
To illustrate take $\nu \to \infty$, $L=1$ from our DMFT (the flow $\frac{d}{dt} \mathbf v(t) = - \left(\frac{1}{P} \mathbf X^\top \mathbf X \right) \mathbf v(t) + \mathbf j(t)$), where we have that the response $\mathcal H(\omega) \equiv \int d\tau e^{-i\omega \tau} \frac{1}{D} \text{Tr} \frac{\partial \mathbf v(t+\tau)}{\partial \mathbf j(t)^\top}$ satisfies the quadratic equation for the **resolvent of a Wishart matrix**
\begin{align}
\alpha^{-1} (i\omega) \mathcal H(\omega)^2 + (i\omega + 1 - \alpha^{-1}) \mathcal H(\omega) - 1 = 0 .
\end{align}
This will give a **distribution over time-constants (eigenvalues)** instead of a single Dirac delta function.
**Missing Experimental Data**
D=1000, we will add.
**Computational cost with Parallelism**
We will include this in the analysis.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for the detailed reply, which has clarified most of my concerns. Accordingly, I raise my score to 4. | null | null | null | null | null | null |
Analyze Feature Flow to Enhance Interpretation and Steering in Language Models | Accept (poster) | Summary: This paper studies sparse autoencoders (SAEs) trained on different layers and modules (residual stream, MLP and attention), proposes using cosine similarity to locate predecessor features in the previous layer given any target feature represented by SAE decoder weights. Through this approach, this paper traces how SAE features evolve throughout the model, and constructs a flow graph that connects features in different layers that allows for effective multi-layer cumulative steering for text generation.
Claims And Evidence: Yes. However, I have the following concerns regarding certain parts of the paper:
- **Section 5.1, Identification of feature predecessors.** The authors illustrate the (statistical) difference between each group of features, categorized by how each feature is co-activated with its predecessors. From Figure 5, it is noted that among the target features examined, **about 60-70%** can be explained as originated from RES or being “created” via MLP/Att. However, I have concerns about this estimand as follows.
- (1) The target feature set is identified through random sampling (Appendix A.1), which might include features that are generally activated but not specific to the dataset considered. To further validate the goal in Section 3.3 of “tracking the evolution of feature”, it would be nice to improve this step by ensuring the features considered are rarely activated on other datasets so they are tailored to the examined distribution. This might also explain why the curves look similar to each other albeit obtained from drastically different datasets.
- (2) It is unclear whether there are preceding features that are co-activated with the target feature with high probability, **but cannot be identified via cosine similarity search.** Thus, it is necessary to examine all preceding features to identify candidates with the highest frequency of co-occurrence with the target feature, and verify if these features truly correspond to the ones determined by the cosine similarity search.
- **Section 5.2, Deactivation of features.** My concern is whether a cascading effect of deactivation could exist, given the discussion in Section 2.3 that “most features in the residual stream remain relatively unchanged across layers”. Specifically, is it possible that a similar feature is reactivated again in later layers, even though it appears to be eliminated when examining the current target feature? My suggestion is to check the downstream features in the constructed flow graph, to determine if such an event occurs.
- **Section 5.3, Model steering.** From Figure 10, how could the conclusion that “cumulative intervention outperforms the single-layer approach” be drawn, given that the blue curve shows a better best score than the orange curve?
Methods And Evaluation Criteria: Yes. The proposed use of cosine similarity has already been adopted for clustering SAE features (e.g., [1]), and in this paper it is taken to examine feature evolution across different layers. The evaluation of deactivation and steering follows the intervention standard of SAEs in current literature.
[1] Scaling Monosemanticity: Extracting Interpretable Features from Claude 3 Sonnet
Theoretical Claims: N/A
Experimental Designs Or Analyses: Yes. For questions, see claims and evidence.
Supplementary Material: Yes, Sections A and B to understand the experimental setup.
Relation To Broader Scientific Literature: This paper provides evidence on how SAE features evolve through different layers. The enabled automatic similar feature search (flow graph) and the following intervention proposal could enhance the quality of model steering and contribute to a better understanding of these models.
Essential References Not Discussed: I have not found essential missing references.
Other Strengths And Weaknesses: The evaluation is comprehensive, and the idea of tracing the evolution of features through SAEs is novel to date.
Though cumulative intervention is claimed to be beneficial, I don’t see the effect significantly, see claims and evidence.
Other Comments Or Suggestions: - Section 2.2 line 055: wrong reference to transcoder
- Section 3.2 line 144: should the topK operation be executed per row, instead of been applied globally?
- Caption in Figure 10: the blue curve is not a multi-layer steering method.
In addition, I strongly recommend that the authors move some essential information from Appendices A and B into the main text. The authors emphasize from the beginning that the technique is “data-free”, without mentioning how the features are selected given a dataset of interest in the main text. Additionally, there are technical details omitted in the main text that are required to understand the experimental results. For example, the labels of “random” and “permutations” and the $r$ parameter in the deactivation experiment and the “cumulative” terminology. For my other concerns, please refer to claims and evidence.
Questions For Authors: Please see claims and evidence.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for valuable questions.
> To further validate the goal in Section 3.3 of “tracking the evolution of feature”, it would be nice to improve this step by ensuring the features considered are rarely activated on other datasets so they are tailored to the examined distribution.
>
We appreciate this suggestion. To address feature specificity, we estimated activation frequencies across 100k non-special tokens from FineWeb and categorized features into quantiles based on their activation rates. As expected, the results vary significantly depending on the quantile selected, supporting the need for careful feature selection.
https://anonymous.4open.science/r/icml_rebuttal-5064/quantiles.png
> It is unclear whether there are preceding features that are co-activated with the target feature with high probability, **but cannot be identified via cosine similarity search.**
>
To evaluate this, we calculated the following score: the fraction of features for which the top-1 match by cosine similarity also appears in the top-*k* matches by Pearson correlation.
https://anonymous.4open.science/r/icml_rebuttal-5064/top_k_corr.png
https://anonymous.4open.science/r/icml_rebuttal-5064/top_k_gpt.png
https://anonymous.4open.science/r/icml_rebuttal-5064/top_k_pythia.png
We observe strong agreement for residual features in Gemma and GPT-2, while MLP and attention features show lower consistency. However, we have not yet validated whether Pearson-based matches reliably predict causal relationships or steering outcomes—a valuable direction for future work, and we thank you for highlighting this.
> is it possible that a similar feature is reactivated again in later layers, even though it appears to be eliminated when examining the current target feature?
>
Yes, this is very common. Since deactivation typically applies only to a small subset of features, and rescaling coefficients are often modest, hidden states undergo only minor perturbations, allowing for later reactivation. We hypothesize this stems from the model’s self-repair mechanisms, which can recover information even after layer pruning (cf. [1–3]). To mitigate this, effective deactivation may require not just zeroing target features but also adding another steering vectors to the hidden state to prevent such recovery (discussed in Appendix C.2).
To test the occurrence of reactivation, we used three strategies: deactivating only the first layer in a graph, deactivating a random layer in a graph, deactivating the first half of layers in a graph. Subsequent deactivations were measured on residual nodes that comes after the deactivated layer, confirming that reactivation is present, but it depends on intervention method and strength.
https://anonymous.4open.science/r/icml_rebuttal-5064/reactivation.png
> From Figure 10, how could the conclusion that “cumulative intervention outperforms the single-layer approach” be drawn, given that the blue curve shows a better best score than the orange curve?
>
Thank you for highlighting this. Cumulative steering generally achieves comparable effects at *lower rescaling coefficients* (Figure 10), improving stability. While single-layer steering can yield higher total scores, it requires either precise selection of highly impactful layers, or spanning multiple layers with a well-constructed feature graph.
This introduces additional optimization challenges not faced by cumulative steering. We will revise this conclusion in the updated manuscript to reflect this nuance.
References:
[1] [Your Transformer is Secretly Linear] (https://arxiv.org/abs/2405.12250)
[2] [What Matters in Transformers? Not All Attention is Needed] (https://arxiv.org/abs/2406.15786)
[3] [The Hydra Effect: Emergent Self-repair in Language Model Computations] (https://arxiv.org/abs/2307.15771)
---
Rebuttal Comment 1.1:
Comment: Thanks for answering my questions.
**Feature specificity.** You stated the frequencies are estimated using 100K FineWeb tokens. If I understand this correctly (please clarify this if I am wrong), you use **features sampled from the datasets you listed in the caption of the Y-axis** and test them on FineWeb tokens to produce the plots. If this is the case, I regard these results as indicating the sampled features in the paper **not dataset-specific**, since on TinyStories and Python Code there are a significant fraction of features that are also activated **frequently** on the FineWeb distribution. I raised this concern because, in Figure 5, the general trend across datasets is consistent, which can be due to the bias of using commonly activated but not dataset-specific features - when examining dataset-specific features (the new plots with lower quantiles), the dynamic change significantly (e.g., for the group of "From RES", it tend to decrease instead of increase). Thus, if the results across the paper are based on the full feature set, the difference between commonly-activated features and dataset-specific features is worth mentioning, because Figure 5 (and subsequent results) only represent results on the first group but not the second (as supported in the new plots). I would strongly encourage the authors to include new results on dataset-specific features, to check if there are other differences in subsequent experiments besides what you have for Figure 5; but I believe requesting these results is beyond the rebuttal period limit, so please take this as a suggestion.
**Preceding features that are not selected through cosine similarity.** I raised this concern because the feature set discovered through cosine similarity can be incomplete, and the added results support this claim, especially for non-From-RES features. This may explain the phenomenon in Section 5.2 where negative rescaling has a strong impact on the From RES features but not MLP/Att ones.
**Reactivation.** I regard this as a partial limitation of the work because this implies the feature flow discovered is incomplete, since deactivating a single (or several) feature does not fully cancel the resulting feature in the end. Given this work as the first to study SAEs for multi-layer understanding and steering, I suggest you add this to the discussion.
---
**Edit:** Thank you for the additional response to my concerns. Let me clarify my question on feature specificity. I understand in Figure 5 all results are derived independently from the datasets specified in the plot titles. However, this cannot guarantee that these features are **dataset-specific** if not filtered (as evidenced in your new experiments during rebuttal). This implies the same trend in Figure 5 could arise due to these commonly activated features. In short, the selection process dedicated to each dataset does *not* imply the set of features is also tailored to the data, as commonly activated features could exist. This is why I suggested checking the results of new experiments and examining when filtering is applied if the dynamic could be different - and it turns out to be true.
Thanks for the additional comparison with the Pearson-based selection. This additionally highlights the data-free proposal. I also understand that the flow captured can be partial. Thanks again for addressing my concerns. I will raise my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your response.
Let us clarify on points you mentioned above.
**Feature specificity.**
To clarify, the features validated in our paper (Figure 5) are derived independently from the datasets specified in the plot titles. For instance, in the Python code analysis, we perform a forward pass on the Python code dataset, collect information about activated features and their groups, and present the results on corresponding graph. This process involves a single pass over the dataset, ensuring that features are calculated independently for each dataset and are not pre-selected based on other datasets. Thus, the features we validate are inherently data-specific.
The frequency plots (available [here](https://anonymous.4open.science/r/icml_rebuttal-5064/quantiles.png)) were constructed as follows: first, we estimate activation frequencies for all features on the FineWeb dataset and build a sets of features within each quantile, denoted as $F_q$. Next, we process the chosen datasets as described above to identify sets of activated features and their groups, denoted as $F_D$, where $D$ is the dataset name. To build the graph, we take intersection between quantile features and dataset features using $F_q \cap F_{D}$. This ensures that for TinyStories and Python Code, we only consider features rarely activated on FineWeb, addressing your requirement: "ensuring the features considered are rarely activated on other datasets."
To fully address your feedback, we will include these results in Appendix C.1, along with graphs using frequencies computed on other datasets. We will also add deactivation experiment on other datasets to Appendix C.2 and reference them in Section 5.2.
**Preceding features that are not selected through cosine similarity.**
We acknowledge that feature interactions identified via cosine similarity may be incomplete, particularly due to inherent reconstruction errors in SAEs. To approximate dependencies, we use a simple heuristic: *“if a feature with a similar embedding activates in a prior module, it is considered dependent.”* While data-dependent Jacobian methods [1, 2] could enhance interaction estimation, we argue that tracing interactions through SAE weights alone remains valuable for practical applications like steering.
Although MLP and attention layers yield fewer features than the residual stream, their explanations remain relevant (Figure 2), indicating meaningful contributions to the model’s behavior despite their smaller feature count.
To assess how close our method is to top performance, we conducted an additional experiment comparing top-1 cosine similarity matching, top-1 Pearson correlation matching, and a full search for maximum achievable performance. The search process deactivates features one-by-one from the residual, MLP, and attention modules, and activation change metric was computed only for target features which group was identified by cosine or Pearson as either From RES, From MLP or From ATT to ensure fairness. With 1,894 features across two layers, each feature deactivated with three methods, we obtain:
| Method | Top-1 Cosine | Top-1 Pearson | Search |
| --- | --- | --- | --- |
| Mean Activation Change | 0.75 | 0.74 | 0.83 |
| Deactivated Features | 65% | 65% | 73% |
The results show that Pearson correlation does not significantly improve upon cosine similarity, as noted in our response to reviewer jyW6, and highlight the value of our data-free strategy for both matching quality and causal analysis. We will include these results, computed on an extended feature set, in Appendix C.2.
**Reactivation.**
Consider a feature $r_i^l$ in the residual stream at layer $l$, which depends on both a feature $m_j^{l-1}$ from the previous MLP layer and a feature $r_k^{l-1}$ from the residual stream at layer $l-1$. Even if $r_k^{l-1}$ is deactivated, $r_i^l$ may still be activated via the alternative path through $m_j^{l-1}$. This illustrates our broader claim: features can be activated through multiple redundant pathways. In our reactivation experiments, we intentionally isolate and test the effect of deactivating one path at a time, acknowledging that this approach does not fully suppress the feature’s activation (due to remaining pathways).
This underscores the complexity of feature interactions and highlights the value of our method in identifying partial dependencies—even if complete deactivation would require targeting all contributing paths. See also discussion in Appendix C.2 about maximum deactivation quality.
Thank you again for your openness to further conversation. If we have addressed your concerns, we would greatly appreciate your reconsideration of our score.
References:
[1] Transcoders Find Interpretable LLM Feature Circuits. https://arxiv.org/pdf/2406.11944
[2] Circuit Tracing: Revealing Computational Graphs in Language Models https://transformer-circuits.pub/2025/attribution-graphs/methods.html | Summary: The paper introduces a new approach to systematically map features discovered by SAEs across consecutive layers of LLMs. By using a data-free cosine similarity technique, the authors trace how specific features persist, transform, or first appear at each stage. This method yields granular flow graphs of feature evolution, enabling fine-grained interpretability and mechanistic insights into model computations.
The authors demonstrate how these cross-layer feature maps facilitate direct steering of model behavior by amplifying or suppressing chosen features, achieving targeted thematic control in text generation. Key contributions are threefold:
- Cross-Layer Feature Evolution: Using pretrained SAEs that can isolate interpretable monosemantic directions, the authors utilize information obtained from cosine similarity between their decoder weights to track how these directions evolve or appear across layers.
- Mechanistic Properties of Flow Graph: By building a flow graph, the authors uncover an evolutionary pathway, which is also an internal circuit-like computational pathway, where MLP and attention modules introduce new features to existing ones or change them.
- Multi-Layer Model Steering: The authors show that flow graphs can improve the quality of model steering by targeting multiple SAE features at once, and also offer a better understanding of the steering outcome.
Claims And Evidence: From my perspective, the following are claims made by the authors (and their evidence), with my personal reasons to mark them as convinced or not:
1. **The authors believe that using a data-free cosine similarity technique can trace how specific features persist, transform, or first appear at each stage.**
Evidence: some previous (Not really convinced)_
From a **theoretical** perspective, this seems reasonable, as previous research has claimed high cosine similarity in nearby layers [1] [2]. Since how polysemantic hidden states are inherited with high similarity, it is reasonable to claim that the linear feature, as its components, are inherited to the next layers. However, from an experimental perspective, _I think the authors should give more illustrations of the cosine similarity results and analysis of features that are mapped to be the same.
2. **The four evolutionary pathways with cosine similarity.**
(Relatively convinced) The clarification of four evolution paths, i.e., translated, processed, newborn, and not related, does in some way make sense. _However, I am curious about the activation patterns. I think the co-existence of activation values or the transference can be further evidence of these claims. e.g., if the feature of "Paris" is activated in two layers with the position predicted with the cosine similarity, this will verify the conclusion of this evolution pathway._
3. **Identification of linear feature circuits**
(Convinced)
4. **The authors observe that two groups may differ with respect to sP if module P is active only in one group (and indistinguishable if P is active or inactive in both groups).**
(Convinced)
5. **Differences arise mainly when a residual predecessor combines with another module, indicating that we might miss other types of causal relations.**
(Convinced?)
_I think this may also come from the normalizations and the relatively low cosine similarity between Res - MLP/Attn._
6. **Deactivating a single predecessor causes a greater activation strength drop if it is a group with a single predecessor, which may indicate circuit-like behavior of combined groups.**
(Convinced)
7. **Different groups react differently to rescaling. Positive rescaling (boosting active features) matters most when residual features mix with MLP or attention. Negative rescaling most strongly affects "From RES."**
(Convinced)
8. **Multi-layer intervention outperforms single-layer steering of the initial feature set, reducing hyperparameter sensitivity.**
(Convinced)
9. **Removing topic-related information early allows later layers to recover general linguistic information, aligning with the ability of LLMs to "self-repair" after "damaging" the information processing flow by pruning or intervention into the structure of hidden states.**
(Relatively Convinced)
I think the conclusion may be right, _but I think a more controllable experiment is needed, following the contrastive construction method from CAA.
[1] https://arxiv.org/abs/2403.17887
[2] https://openreview.net/forum?id=XAjfjizaKs
Methods And Evaluation Criteria: Based on my understanding, the methods and evaluation criteria proposed in the paper seem to make sense for the problem and application at hand. Here's a breakdown:
**Problem:** The paper addresses the challenge of interpreting and controlling the behavior of LLMs. Specifically, it aims to: (1)**Improve interpretability** (2) **Enable steering**.
**Proposed Methods:**
- **Data-free cosine similarity:** This method is used to track the evolution of features across layers. As discussed in Claims And Evidence 1, I think the authors should give more illustrations of the cosine similarity results and analysis of features that are mapped to be the same.
- **Feature flow graphs:** These graphs visually represent how features evolve across layers. This is a helpful tool for providing a clear and intuitive way to understand the complex interactions between features.
- **Multi-layer steering:** This technique leverages the feature flow graphs to control model behavior by intervening on specific features across multiple layers.
Theoretical Claims: I have checked the correctness of proofs about the feature matching, evolution of feature, and activation of theme. I believe they are theoretically correct.
Experimental Designs Or Analyses: Based on my review, there are some points that could be strengthened or clarified:
1. The paper relies heavily on cosine similarity to map features across layers. The choice of threshold for determining whether two features are related could be further justified. I suggest the authors could explore the sensitivity of their results to different threshold values and provide more analysis on how the threshold was selected.
2. The paper demonstrates successful steering in specific scenarios. However, it would be helpful to explore the generalizability of the steering method to a wider range of tasks and topics.
Supplementary Material: As part of the review process, I examined the supplementary code provided by the authors, who remained anonymous.
Relation To Broader Scientific Literature: 1. The method provides a straightforward way to identify and interpret the computational graph of the model without relying on additional data.
2. To my acknowledgement, the authors are the first to use SAE features from different layers to control LLM generation.
3. The improved controllability has positive implications for alignment, interpretability, and safe deployment of AI systems, as it can allow developers to steer models away from harmful or biased outputs
Essential References Not Discussed: None.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: I have no further suggestions to this paper.
Questions For Authors: 1. Some layers share less cosine similarity with others, e.g., the first layer; does this affect the mapping/steering?
2. More charts/graphs about the dynamics of cosine similarity?
3. Can the co-existence of activation values or the transference be further evidence of the evolution claims?
4. How about the sensitivity of the steering results to different threshold values? And
5. How was the threshold selected?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your insightful comments and questions.
> 1. Some layers share less cosine similarity with others, e.g., the first layer; does this affect the mapping/steering?
We observe that layers indeed vary in feature-matching quality, though we have not yet quantified this systematically (e.g., via similarity analysis of feature descriptions). Your suggestion to assess this further is valuable, and we will incorporate such analysis to strengthen our paper.
Notably, we find that certain layers (e.g., the 4th, 9th, and 18th in Gemma) exhibit differences in how well features match their top-1 similar counterparts in the MLP versus the previous residual stream. This aligns with feature clustering patterns, as shown in Figures 3 and 18b: early layers lack strong cluster separation, leading to poorer matching, while later layers converge toward a single dominant cluster with less distinct groupings.
https://anonymous.4open.science/r/icml_rebuttal-5064/out_mlp_scatters.png
https://anonymous.4open.science/r/icml_rebuttal-5064/out_attn_scatters.png
We have not identified generalizable differences in steering effectiveness across layers, as our analysis so far has focused on a limited set of features and graphs. However, we note that steering MLP or attention features often produces negligible effects, regardless of the target layer or steering coefficient. We hypothesize that this could stem from imperfect matching or the possibility that these features operate differently (e.g., requiring other active features in the residual stream to function). Further investigation is needed here.
> 2. More charts/graphs about the dynamics of cosine similarity?
>
We have measured the mean cosine similarity between hidden states at layer outputs and three SAE-related positions, plotted against relative layer distance:
https://anonymous.4open.science/r/icml_rebuttal-5064/cossim_models.png
The divergence in Pythia’s results may arise from its parallel residual stream architecture: $\text{Layer}(x)=x+\text{MLP}(\text{norm}_1(x))+\text{Attn}(\text{norm}_2(x))$. We hypothesize that higher cosine similarity between hidden states correlates with better matching quality, though this depends on SAE and model architectures—an aspect we plan to explore further.
These findings may also explain why steering MLP and attention features is less impactful than steering residual features. For additional results on correlation matching and group dynamics in Pythia and GPT-2, please see our response to Reviewer jyW6.
> 3. Can the co-existence of activation values or the transference be further evidence of the evolution claims?
>
Yes. If you refer to transference across forward layers, we find that matching via the residual stream generally works well, whereas matching with MLP or attention features in the next layer is often poor. We have prepared example graphs of activations for specific texts, available at.
https://anonymous.4open.science/r/icml_rebuttal-5064/g_3_t_0.5.png (g_3_t_0.8.png/g_3_t_0.85.png)
> 4. How about the sensitivity of the steering results to different threshold values?
The steering effect varies significantly depending on the graph and target feature. For instance, steering the "London" feature barely influences London-related tokens unless the coefficient is very high, at which point it introduces fashion-related terms (see [1] and Appendix E). Some features even show minimal response to steering.
Thus, different graphs react differently, and a systematic study of threshold sensitivity would require extensive experimentation across many features and setups. While we did not aim to optimize thresholds (given their dependence on model/SAE architecture, SAE quality, etc.), we acknowledge this as an important direction for future work.
For our steering experiments:
- Deactivation did not use thresholds, i.e. full graphs from 0th to 25th layers were used.
- Activation thresholds were chosen empirically: higher thresholds sometimes diluted the theme by including weakly related features, while lower thresholds reduced theme prominence.
> 5. How was the threshold selected?
Initially, we derived thresholds from feature group analysis (Section 5.1) and correlation studies. For example, in Gemma’s 18th layer, we colored features with >0.65 correlation to MLP (orange) or residual (blue) features, then applied linear separation:
https://anonymous.4open.science/r/icml_rebuttal-5064/thresholds.png
For experiments, we determined thresholds $s^{(R)}=0.5$ and $s^{(M, A)}=0.15$ by computing feature activations across texts, building graphs with active features highlighted, and by manually examining those graphs for threshold values that preserved semantic consistency and co-activation of features in graphs. While expert input remains helpful, we believe this process could be automated in future work.
[1] https://arxiv.org/pdf/2411.02193
---
Rebuttal Comment 1.1:
Comment: Thanks for your detailed response. Most of my concerns have been addressed. I have revised my assessment accordingly. | Summary: The authors introduce a method to allow for cross layer and mulit-module (mlp, residual stream, attention block) level mapping of SAE based features, creating a flow graph using a data-free cosine similarity technique (between feature embeddings and encoder blocks), that allows a person to interpret and trace how specific features persist, transform, or first appear across layers. The paper analyzes such feature evolutions on GemmaScope and LlamaScope SAEs and models and also demonstrates how their method facilitates cumulative layer wise direct steering of model behavior by amplifying or suppressing chosen features for targeted control in text generation and potential causal circuit discoverability.
## update after rebuttal
While the paper provides an interesting method by which to do cross layer, multi-module analysis, and the authors have said they will address the concerns I stated ( which are largely organizational and for clarity), without seeing the revisions and organization changes ( which will be substantial ) its hard to move the current overall recommendation.
Claims And Evidence: The main methodological proposals/claims made by the paper involve:
1. cosine similarity based feature matching (section 3.2),
2. tracking the evolution of features across modules (mlp, res, att) (section 3.3),
3. 4 heuristics for understanding patterns seen over similarity scores for features/modules (translating, processing, new born and not explained by method) (3.3),
4. discovering long range feature flows by composition of short range matching over consecutive layers (section 3.3)
5. Identification of linear feature circuits / flow graphs ( section 3.4)
6. Model steering at the flow graph level
The points overall are well motivated and backed up, however points 1, 3, and 5 lack some supporting evidence in the main body of the paper that could help with clarity.
Point 1, section 3.2 is quite clear and easy to follow, however the corresponding results section 5.1 “Identification of feature predecessors” was less so.
(Q1) For Fig 4, what are the raw counts of these groups before looking at differences? its hard for me to understand 4 in general and that may help, but from this figure i mostly see that most groups similarity scores are stats sig different (with the slight exception of ATT where AB group has lower s(A) , but still above 75%).
(Q2) In Lines 316-19 how can you tell if features are emergent from Fig 5 alone? In terms of “propagating from preceding layers” do you mean because “From Res” goes up? it might help to have a guide to reading this graph to make it more clear.
(Q3) Lines 326-329 make references to differences in dataset in latter layers, but its hard to tell from graph alone of any differences as they look relatively the same to me?
(Q4) LlamaScope is mentioned in the models section 4.1 and mentioned in one line in section 5.1 (which itself points to Figure 18b in the appendix). Because its relegated to the appendix, i didn’t notice that the Gemma and Llama are quite different over all ( see From Res relationship to other lines in both for instance).. How is this difference explained ? Discussion comparing findings on these two models and their SAEs should be expanded as they seem fairly central to any generalization claims for point 1
(Q5) Throughout, its appreciated you include a “not explained” heuristic ( heuristic D in section 3.3), but discussion on what might be causing “from nowhere” to be the highest scoring pattern observed throughout in Fig 5 and Fig 18b?
Point 3, in 3.3 in describing the heuristics section for phenomena that can be explained, the phrases used are “the feature likely exists …”, “the feature was likely processed ..”, and “the feature may be newborn ….” , and the experiment results assume these heuristic short hands to be true in a way that is difficult to assess. (Q6) Is there anyway to validate these short hands?
Point 5 ( section 3.4 ) is said to be validated in experiments and Appendix E while the appropriate experiment setup section 4.2 “deactivation of features” which I think allows for casual circuit claims says to look at Appendix A for experimental matching strategies and metrics quantifying effectiveness. The appropriate results section ( 5.2 deactivation of features ) makes reference to rescaling coefficient r ( not mention in the main body of the paper ). (Q7) For clarity the appropriate context/setup needs to be introduced in the main body of the work and towards that end the findings related to Figure 7 (which while interesting don’t seem central to the papers main claims) seem like they could be moved to the appendix and you could use the space gained to give more setup for deactivation in 4.2?
(Q8) Its unclear how Figure 10 shows that cumulative intervention outperforms the single layer approach? It seem reasonable to say that for layers 18 on this true, but not for early ones? Is my understanding correct? If not, this should be expanded/clarified.
(Q9) Also in the caption of Figure 10, the orange and blue lines are said to be multi-layer interventions while in the legend of the Fig 10 (RHS) blue is said to be One Layer?
(Q10) In Figure 11 ( single, constant, exponential, linear ) steering approaches are shown without being explained in the main body of the paper? Precise details are fine for the appendix, but setup and metrics needed to understand figures in the main body of the paper should be explained in the main section so that the paper is self contained.
(Q11) In reference to lines 420 and 421, “We conclude that multi-layer interventions indeed affect the model more than single-layer approaches “, given my questions on Fig 10 and Fig 11 this is not very clear to me.
Nit:
Line 191, R == R_L-1 was a little confusing as a convention to me. its explained clearly later so maybe just use R_L-1 alone instead?
Overall the method is reasonable and the findings are interesting, but it seems selecting the more important findings to highlight and focus on and moving some of the others out to the appendix for space could benefit clarity.
Methods And Evaluation Criteria: Proposed and evaluation criteria are mostly reasonable. See Claims And Evidence section on questions and suggestions for how to improve clarity.
Theoretical Claims: N/A
Experimental Designs Or Analyses: Proposed and evaluation criteria are mostly reasonable. See Claims And Evidence section on questions and suggestions for how to improve clarity.
Supplementary Material: I went through much of the extensive appendix. I did not look at the code.
Relation To Broader Scientific Literature: This work introduces a novel interpretable data-free method for multi-layer steering, which enables the tracking of concept evolution across layers and the identification of computational circuits through targeting the weights of pretrained SAEs.
Essential References Not Discussed: None outside of the 4 month window for concurrent works that I know of.
Other Strengths And Weaknesses: This work introduces a novel interpretable data-free method for multi-layer steering, which enables the tracking of concept evolution across layers and the identification of computational circuits through targeting the weights of pretrained SAEs. While there are some issues with clarity, overall the method could allow for expanded analysis of models leveraging SAEs at th moment.
See Claims And Evidence section on some improvements needed for clarity and setup of some experiments. Future work would need to address newer work (https://arxiv.org/abs/2501.17727) showing SAEs can interpret randomized vectors and the need to tie them to downstream performance in order for them to be grounded.
Other Comments Or Suggestions: See Claims And Evidence section for comments/suggestions.
Questions For Authors: See Claims And Evidence section on questions
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your careful reading and insightful questions.
---
**Q1.** The purpose of Figure 4 is indeed to show that these groups differ significantly. Below are the raw counts of elements in each group:
| Nowhere | RES | MLP | ATT | RES & MLP | RES & ATT | MLP & ATT | RES&MLP&ATT |
| --- | --- | --- | --- | --- | --- | --- | --- |
| 3396295 | 2338643 | 972662 | 574635 | 769450 | 606080 | 261068 | 308578 |
See Figure 13 for an evaluation of how frequently groups intersect. Those values are calculated as $|G_1\cap G_2|/|G_1|$, where $G_1$ is a row group and $G_2$ is a column group.
**Q2.** Figure 5 alone cannot confirm feature emergence. We instead analyze group proportions across layers. Features are classified as *emergent* if closer to module (MLP/ATT) features than residual stream features (Figures 12b, 18c), placing "From MLP", "From ATT", and "From MLP & ATT" in this category. *Translated* features are those closer to the previous residual stream ("From RES"). See also our answer to Q6.
**Q3.** Comparing FineWeb and Python Code in the later layers reveals a higher presence of “From nowhere” features than “From RES,” distinguishing this dataset from others. The same trend appears for Llama (see Figure 18b) and Pythia-70M (mentioned in our response to reviewer jyW6).
**Q4.** We may have misparsed your comment—did you mean "I did notice"? Model differences exist but stem from varying architectures, parameter counts, and SAE training procedures. A full explanation requires deeper study (e.g., identically architected SAEs on shared data). We will provide additional discussion and experiments on Pythia and GPT-2 in the revised manuscript to address this further.
**Q5.** We believe there are two primary causes for features labeled “From nowhere.” First, there may be a matching error—artifacts from SAE training or a situation where the true predecessor is not the top-1 but perhaps the top-2 or top-3 similar feature. Second, some features could be combinations of two or more features, making them harder to detect via a simple top-1 match; they could also transform (e.g., rotate) as they pass through the layer, as reviewer jyW6 pointed out. Using top-5 cosine similarity, as in our deactivation experiment, reduces the “From nowhere” group substantially, but it is unclear if it can ever be made negligible. Expanding the SAE dictionary might also risk increasing false positives under the top-1 strategy, so this trade-off requires more investigation. We will extend our discussion of the “From nowhere” group to clarify these points in the revised version.
**Q6.** We currently think of two general approaches for validating these shorthands.
The first involves analyzing their semantics and activation patterns. For instance, if a target feature activates on tokens like *“the, a”*, while its predecessor in the residual stream fires on *“the, The”* and the corresponding MLP feature activates on *“a, A, an”*, this suggests the target feature emerges from their interaction—we categorize it as *“processed.”* Features with nearly identical descriptions and activation patterns across layers likely belong to the *“translated”* group, indicated by high $s^{(R)}$ values. Conversely, features without semantic ties to the residual stream but aligned with MLP or attention counterparts may be *“newborn”*—new linear directions introduced by those modules. Expanding this analysis beyond top-1 matches (e.g., to top-5) could further enhance its reliability.
Figures 3 and 18b illustrate clusters in the top-left corner, where features lack $s^{(R)}$-similar predecessors in the residual stream. This could imply either new feature introduction by the MLP (e.g., stored knowledge) or transformation of an initially dissimilar residual feature via MLP processing. In contrast, Figure 5 shows a clear predominance of the ”From RES*”* group, suggesting most features propagate across layers with minimal modification.
While this analysis could be automated, it hinges on either reliable feature explanations or raw activation data.
The second approach tests feature roles through steering experiments. For example:
1. Steering only the target feature,
2. Steering its residual predecessor, or
3. Steering the residual predecessor while deactivating active MLP/attention predecessors.
Comparing these setups could reveal mechanistic differences, though we have not yet implemented this systematically. Preliminary versions of (a) and (b) appear in Section 5.3, though (b) in our current work involves steering the entire flow graph, not just the residual stream.
---
Rebuttal Comment 1.1:
Comment: Thank you for clarifying and answering most of the questions I've listed ( Q1- Q6). Point 5 (Q7) is particularly important for the overall clarity of the paper so I hope you'll be able to address that.
---
Reply to Comment 1.1.1:
Comment: We sincerely apologize for the inconvenience regarding the remaining questions: we encountered issues with formatting the rebuttal in time, resulting in it being cut short. Below we briefly answer other questions and outline our plan considering the improvements of clarity and presentation:
**Q7.** We agree that the main body should contain those details and will improve the structure by making the following improvements:
- We will extend 4.2 by a) introducing the rescaling coefficient, b) briefly describing matching strategies and c) explaining our activation change metric; considering steering experiment, we will d) clarify the single-layer/cumulative terminology, e) the baseline approach we compare our method with, f) explain our evaluation strategy and g) briefly describe the three cumulative steering approaches (constant, linear, exponential).
- As you rightfully pointed out, results and text regarding Figure 7 would be better placed outside the main text, and we will move them into Appendix C.2.
- We will improve conciseness of the Results section by removing redundant explanations that should be given in 4.2, such as the first paragraphs of 5.2 and 5.3.
**Q8 & Q11.** Cumulative steering outperforms single-layer steering in terms of requiring lower rescaling coefficients, which improves stability, while single-layer steering, as indicated by the total score, can be more effective overall but demands either spanning multiple layers with a reliable graph or selecting particularly impactful layers, which introduces additional hyperparameter dependency. Thank you for highlighting this, we will revise these descriptions for clarity, both in the Results and Discussion section.
**Q9.** By “multi-layer,” we intended to encompass both cumulative and single-layer approaches (since we can potentially find related features in other layers), as opposed to *single-feature* steering. We would also clarify that.
---
We appreciate the time and effort you dedicated into reviewing our paper. We will gladly incorporate results of this discussion and improve the clarity and presentation of our paper, and we hope that we have addressed your concerns and you find our responses satisfactorily. If so, we would be deeply grateful for your support of our paper. Thank you again for your thoughtful review. | Summary: The paper investigates whether features in LLM activations identified by SAEs trained on individual activation locations - namely residual streams, attention outputs and MLP outputs - can be linked to one another, so that we can, broadly speaking, try to answer questions like "where did a feature come from?" and "how did a feature evolve through the layers?".
Features across SAEs are linked to each other via the cosine similarity of their decoder vectors. Specifically, given:
- a residual stream SAE feature $f$ in layer $L$;
- SAEs trained on the previous residual stream of layer $L-1$, as well as the MLP and attention outputs in-between;
we define $s^{(R)}, s^{(M)}, s^{(A)}$ to be the top cosine similarities of $f$ with any decoder vector in the previous resid (R), MLP (M) and attention (A) SAE decoder vectors. The relative magnitude of these values is used to classify a feature as being one of:
- translated from the previous residual stream without MLP/attn involvement;
- processed by the MLP or attn when all values are high
- "newborn", created by the MLP or attn
- unexplained when all values are low.
The main body experiments aim to answer the following questions:
- **feature predecessors**: this checks that feature predecessors identified using the paper's method correlate with SAE feature activation, i.e. if the predecessor of $f$ activates on a datapoint, does $f$ activate too?
- **deactivation of features**: if we deactivate a predecessor feature of $f$ by subtracting it from the activation, will this lead to $f$ not activating?
- **model steering**: can we improve upon naive single-layer steering by steering multiple features across layers jointly when they're identified as connected via predecessor relations?
The results suggest the following:
- we generally observe a clear cluster of features that have a strong predecessor in the preceding MLP layer but not in the previous residual stream layer, and for these features it's also generally the case that if the feature is active, its MLP predecessor is also active. By contrast, for attention we see no such pattern.
- feature deactivation guided by cosine similarity performs significantly better than a baseline using random choice. Deactivation seems to have higher impact on activations when done using residual stream predecessors vs MLP/attn predecessors.
- for steering to activate a certain topic in the generation, results don't clearly show that the proposed methods outperform baselines or single-layer steering. For steering to de-activate a topic, i.e. suppress mentions of it, there seems to be some benefit to multi-layer steering versus single-layer.
## Update after rebuttal
The rebuttal has not meaningfully changed my assessment of the paper. Despite other issues, I hesitate to recommend acceptance mostly because I don't see a strong motivation behind the problem being studied and don't see the usefulness of the results to the broader field of interpretability.
Claims And Evidence: In general, the claims made in the paper are supported with evidence reasonably well, however there are some issues with the methodology and presentation of results (described below and in subsequent sections) that make it difficult to evaluate the scope and novelty of the findings.
- a key property of the methods in this paper is that they can only tell us about how the same feature persists (or not) through layers, or when it "appears".
- This limits the conclusions that can be drawn from the results; by contrast, a much more interesting (and more difficult) question would be to understand how different features combine through attention and MLP blocks to create *new* features.
- Furthermore, the approach in this paper fails to fully account for the possibility that features "rotate" across layers, as described e.g. in https://transformer-circuits.pub/2024/crosscoders/index.html; to some extent, this is mitigated by linking features through successive layers, but it is unclear if this overcomes the problem. I think that a careful study using a tool similar to cross-coders, as well as comparing feature activations over datasets of texts, could help answer this question.
- in general, the methods and claims may be shedding more light on the geometric structure of the SAE matrices as opposed to the workings of the model. For instance, it has been observed that SAE encoder and decoder vectors for the same feature have substantial though not perfect cosine similarity (see e.g. https://transformer-circuits.pub/2023/monosemantic-features#comment-nanda). This alone *may be* enough to explain the results on predecessors and deactivation!
- in general, the paper would have benefited from more methods and experiments that establish the relevance of the phenomena explored to the end-to-end behavior of the model, as opposed to internal geometric structure that may be an artifact of SAE optimization. The steering experiments are one promising step in this direction.
- it should be noted that while the cosine similarity method is advertised as "data-free", the features we're taking the cosine similarity of themselves came from SAEs, which are trained on vast amounts of data. So strictly speaking this is not a data-free interpretability method (as opposed to a method that is purely based on the weights of the model). In general, "data-free" interpretability methods have the promise of explaining the out-of-distribution behavior of a model precisely because they are independent of any properties of the data apart from what is encoded in the model weights, which is a key motivation for considering such methods. However, this motivation does not really apply to the methods in this paper. However, it should be noted that truly data-free methods have so far struggled to provide useful interpretability insights.
Methods And Evaluation Criteria: Some shortcomings:
- there is a lack of a baseline approach for linking features to one another across layers that the approach of the paper can be compared to. The top candidate that comes to mind is an activation-based metric that correlates feature activations over a large set of examples.
- in general, there is often not enough detail to get a full picture of how a given method is implemented.
- a potential source of noise for the given methodology is that it is known that SAEs trained on the same activations can arrive at different features with different random seeds. See the paper "Sparse Autoencoders Trained on the Same Data Learn Different Features" by Paulo and Belrose. In the absence of any "anchor" between different layer SAEs, linking features in such a naive way may be suboptimal; a strong activation-correlation baseline is desirable.
- the way in which behavioral and coherence scores are assigned in the steering experiments is not explained.
- combining behavioral and coherence scores in a single metric is a potential source of misconceptions and illusory results. Furthermore, doing so via multiplication is not very principled: what's the interpretation of a unit in the resulting scale? It feels overly confusing to think about that. A very high behavioral score can be achieved at moderate coherence if the model repeats a phrase related to the topic. In general it's more insightful to look at both behavioral & coherence metrics together on a 2D plot.
Theoretical Claims: N/A
Experimental Designs Or Analyses: - In general, for many of the experiments and figures there is insufficient detail describing what is being done/visualized.
- I don't quite follow Figure 7. Is "activation change" measuring the drop in the SAE feature's pre-activation? Also, if we're deactivating 1 predecessor at a time, where is it shown how the effect evolves with the number of predecessors deactivated? Also, how do we get multiple predecessors for a feature? Do we just look at the top k highest cosine similarities?
Supplementary Material: N/A
Relation To Broader Scientific Literature: It's hard to situate the contributions of the paper in the broader literature because of the lack of baselines and the possibility that many of the results follow from known facts about SAE encoder/decoder geometry. The exception is the steering experiments, which may be a useful addition to the literature, especially if presented in more detail / with easier to interpret analyses (see previous points).
Essential References Not Discussed: - in the discussion of the topk activation function, a foundational reference that for the first time proposed the use of this activation in SAEs and established its improved metrics and scaling properties is missing: Gao, L., la Tour, T.D., Tillman, H., Goh, G., Troll, R., Radford, A., Sutskever, I., Leike, J. and Wu, J., 2024. Scaling and evaluating sparse autoencoders. _arXiv preprint arXiv:2406.04093_.
Other Strengths And Weaknesses: Weaknesses:
- The presentation of the methods is confusing (also see comments/suggestions section below). In particular, the "Results" section is actually the one that describes the methods in sufficient detail, whereas previous methods sections only vaguely point at what's going to be done.
- You say "We found that cosine similarity between decoder weights is a valuable similarity metric, and we focus on this approach." (line 160), but this is never justified in terms of alternative methods and metrics. It would be a valuable addition to the paper.
- You say in 3.4. that your method can detect when MLP or attn *remove* features from the residual stream, but there's no evidence for what removal would look like in the paper?
- The 4 subplots of Figure 5 are basically identical - maybe just include 1 in the main body, and say that for other datasets it looks basically the same. Furthermore, this suggests that these lines are more a geometric property of the ensemble of SAEs as opposed to a data-specific property.
Other Comments Or Suggestions: - Section 3.1. feels somewhat redundant, given the introduction which already establishes the motivation? Consider adding a brief sentence to the introduction citing the main relevant works describing the motivation, and cutting this section.
- I think the exposition would flow better if it is stated upfront that we assume that the decoder vectors have unit norm (lines 139 and 140, right column)
- Sections 3.4 and 3.5 are quite vague in terms of methodology; are they really necessary? I don't feel like I got much out of them beyond "we do some cool stuff". Maybe cut & incorporate in later sections that flesh out these ideas?
- Same applies to some extent for 4.2.; I wonder if presentation would be better if there was a single place in the paper that has a 1-sentence brief intuition for each experiment + a very concrete description?
Questions For Authors: - it is customary to subtract the decoder bias $b_{dec}$ from $h$ before applying $W_{enc}$ (cf line 77, left column). Omitting this changes the architecture of the SAE, though in principle the bias can be absorbed in the encoder bias by changing $b_{enc}$ to $b_{enc} -W_{enc}b_{dec}$.
- what is the matrix norm in line 87 (right column)? I assume Frobenius
- in 2.3., is the intention that $B<A$?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your valuable and extensive review. We aim to address your concerns below.
**Claims And Evidence**
Our work examines SAEs at various points in the model and linking their features allows us explore its computational structure—such as the technique described in Appendix F, which mimics a transcoder approach. Thus, we can shed more light on the model’s behavior than just geometry. Permutations [2], top-1 correlation [3], and top-1 cosine similarity (our work) are all special cases of this feature mapping approach.
We respectfully disagree with labeling our approach as non-"data-free", since we use this term following the prior work [2]. While SAEs could be trained on the LLM’s data, we solely analyze model weights, not external data, justifying the "data-free" description.
**Methods And Evaluation Criteria**
We appreciate your suggestion for a data-driven baseline. While useful, such methods struggle with sparse SAEs, demonstrating the advantage of our data-free approach where adjusting k in top-k matching can better address these limitations.
We tested Pearson correlations on 100K non-special tokens from the FineWeb “default” subset for each feature in Gemma Scope’s even layers and all layers of Pythia-70M-Deduped and GPT-2. Using 500 samples (instead of 250) as described in Appendix A.1, we identified feature groups.
https://anonymous.4open.science/r/icml_rebuttal-5064/gemma_corr_cos.png
https://anonymous.4open.science/r/icml_rebuttal-5064/pythia_corr_cos.png
https://anonymous.4open.science/r/icml_rebuttal-5064/gpt_corr_cos.png
Correlation-based matching reduced the "From nowhere" group and better identified attention module predecessors, although the mismatch with Gemma Scope SAEs still lowered quality. For Pythia, results aligned closely with Llama Scope, reflecting clearer attention features.
However, correlation-based matching did not consistently outperform top-1 cosine similarity and performed worse on out-of-distribution Python code (further from FineWeb). Top-1 cosine and top-k correlation predecessors showed strong agreement for Gemma Scope and GPT-2 residual SAEs but weaker alignment for module-based SAEs, consistent with prior feature propagation findings.
These results broadly characterize correlation-based performance. We plan to include these comparisons but welcome requests for specific details to enhance our discussion.
Behavioral and Coherence scores follow the setup from [1], with details and the system prompt described in Appendix B. In brief, we ask a model to assess whether a specific theme is present (Behavioral) and to rate the text’s language quality (Coherence), assigning each an integer score from 0 to 5. These scores are then normalized to the [0, 1] range. We acknowledge that this explanation belongs in Section 4.2 and will revise it accordingly.
As you noted, multiplying the scores ensures that moderate Coherence and high Behavioral (or vice versa) results in a moderate overall score as expected. Both scores are illustrated in Figure 9.
**Experimental Designs Or Analyses**
We define the activation change as $1-\mathbf{z}^{new}/\mathbf{z}^{old}$, where $\mathbf{z}$ is a feature activation after applying JumpReLU.
Each feature may have up to three predecessors (residual, MLP, attention). To identify active predecessors, we use four methods (Appendix A.2).
For features with active predecessors in both residual (R) and MLP (M), we label them “From RES & MLP” and run forward passes deactivating R, M, or both (“deactivated one at a time”). In top-k method, up to five features may be deactivated per predecessor (though few are typically active).
Figure 7 subplots group results by predecessor type; bars show deactivation effects (e.g., deactivating “mlp” in “From RES & MLP” yields ~0.25 mean activation change).
**Other Strengths And Weaknesses**
While we did not explicitly justify cosine similarity as a metric early on, Section 5.2 and Appendix F compare it with a permutation-based method.
By “removal” or “suppression,” we refer to specific linear combinations of features (e.g., “king – man”), similar to combinations that create new semantics (e.g., “woman + power”). We suspect these combinations are common.
**Questions For Authors**
We use the L2 norm, treating vectors as sliced decoder columns.
While our presentation assumes B < A, this is not strictly necessary.
Thank you again for your valuable feedback. We will reorganize our paper, improve clarity, and add the missing reference. We hope these clarifications sufficiently resolve your concerns and encourage you to reconsider your evaluation. Thank you for your time, and please let us know if you have any further questions or requests.
References:
[1] https://arxiv.org/pdf/2411.02193
[2] https://arxiv.org/pdf/2410.07656
[3] https://arxiv.org/abs/2410.08869 | null | null | null | null | null | null |
LaCache: Ladder-Shaped KV Caching for Efficient Long-Context Modeling of Large Language Models | Accept (poster) | Summary: the paper presented a training-free KV cache optimization, named LaCache, for long-text generation tasks. the proposed framework employs ladder-shaped KV cache storage pattern and an iterative compaction mechanism to enable LLMs to better capture long-range dependencies, optimize memory usage, and sustain continuous generation. the authors evaluated the proposed framework by some experiments.
Claims And Evidence: the experimental results show that the proposed framework is effective. However, the improvement is not significant.
Methods And Evaluation Criteria: More datasets should to be used in the experiments. For example, Needle-in-a-Haystack, and RULER benchmarks.
Theoretical Claims: No theoretical claims is shown in this paper.
Experimental Designs Or Analyses: the authors should evaluate the proposed method on more benchmarks, such as Needle-in-a-Haystack, and RULER.and on recent baselines.
Supplementary Material: the paper doesn't provide supplementary material.
Relation To Broader Scientific Literature: incremental work
Essential References Not Discussed: no
Other Strengths And Weaknesses: the main weakness of the paper is that it lack of theoretical analysis and discussion.
Other Comments Or Suggestions: No
Questions For Authors: 1. the rationale of Ladder-Shaped KV Cache Pattern is not convincing. Theoretical analysis and discussion should be provided. I don't fully understand why the authors presented the two formulas in page 4. The formulas don't provide convincing theoretical support for the proposed method.
2. What is the KV cache budget for LaCache in Figure 7?
3. As shown in Figure 7，LaCache is not superior to TOVA. TOVA have remarkable advantage on F1 score while its throughtput is about 17.5, which is not much smaller than 30 (that of LaCache).
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thank you for your time and constructive suggestions! We have addressed all your comments and suggestions as follows.
---
**Q1. Evaluation on more datasets: Needle-in-a-Haystack (NIAH) & RULER**
Following your suggestions, we have added experiments on the NIAH and RULER datasets. Please check our [response to Reviewer fB6E's Question 1](https://openreview.net/forum?id=SDjZtxDo35¬eId=jrewAScmqH).
---
**Q2. Add more KV cache compression baselines**
Following your suggestions, we have added comparisons with SnapKV[1] and PyramidInfer[2] on the entire LongBench dataset, as shown in [this figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ). This set of results consistently validates that LaCache achieves better score-throughput trade-offs than various baselines.
---
**Q3. Comparison with TOVA in Figure 7**
First, we humbly clarify and emphasize that one highlight of LaCache is its simplicity and seamless integration with the existing FlashAttention implementation, as validated by our method’s improved accuracy over baselines under the same real-device efficiency.
Following your suggestion, we conducted experiments comparing with TOVA under more various cache budgets in [figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ). These experiments demonstrate that LaCache achieves better average scores than attention-based methods by a large margin under the same real-device throughput.
---
**Q4. The KV cache budget for LaCache in Figure 7**
We benchmarked our method against different baselines under budgets ranging from 20% to 50% in the original Figure 7. Additionally, our [updated Figure 7](https://ibb.co/q3GrqCZQ) includes more baselines and a wider range from 20% to 99%.
---
**Q5. The rationale and theoretical analyses of the ladder-shaped KV cache pattern**
We humbly clarify that the analysis on Page 4 of our manuscript is intended to provide a high-level rationale for why LaCache is effective rather than serving as theoretical proof. This analysis demonstrates that the ladder pattern can cover potentially important tokens more effectively under the same token budget, thus enhancing the lower bound of information retention, particularly when compared to assigning the same KV tokens across all layers.
This analysis has been appreciated by @Reviewer cTxa, who recognized it as offering “good insights” and showing “a deeper understanding of the problem.” Additionally, as noted by @Reviewer fB6E - “I particularly like the analysis described by Figure 3, where the caching pattern is compared to randomly chosen caching patterns across cache sizes”, we have empirically verified that the proposed KV cache is robust and close to optimal. Specifically, in Figure 3 of our manuscript, we randomly generated over 1,500 patterns under different KV cache sizes to explore all possible configurations where the proposed ladder pattern lies on the Pareto optimality boundary.
In summary, this work primarily aims to (1) empirically demonstrate that our method lies on the Pareto frontier, consistent with the evaluation protocols of most KV cache compression methods, and (2) provide the generalizable insight that the same KV token does not need to be maintained across all layers. A more rigorous theoretical proof of our method is planned for future work.
---
**Q6. Regarding “incremental”**
We humbly clarify that, given the increasing need for LLMs’ long-context capability in more real-world AI serving systems and applications, simplicity is a key highlight and design consideration of our proposed method. In particular, our proposed technique can (1) be seamlessly compatible with FlashAttention without introducing extra overhead during inference and (2) offer generalizable insights to guide future KV cache designs—i.e., the same KV token does not need to be maintained in all layers, and the ladder pattern is an effective way to achieve this by improving the lower bound of information retention to cover potentially important tokens. This has been positively recognized by @Reviewer cTxa, who noted, “The effort for building LaCache’s practical considerations is very helpful as it could be deployed easily with existing systems. Great to see the compatibility with systems such as Flash Attention. Very promising work.”
Finally, we wish to emphasize that developing a simple yet effective technique like LaCache is nontrivial, given the extensive research already conducted in this area. This sentiment is echoed by @Reviewer fB6E, who noted, “This is a crowded space, but I think this is a nice contribution and argues its point well.”
---
Thank you for your thoughtful suggestions and comments that aim to help strengthen this paper! If you have any further questions or updated comments, we would really appreciate and be happy to address them.
---
**References**
[1] SnapKV: LLM Knows What You are Looking for Before Generation
[2] PyramidInfer: Pyramid KV Cache Compression for High-throughput LLM Inference | Summary: This paper proposes a method to compress KV cache with the goal of storing different sets of tokens in different layers, termed Ladder-Shaped KV Cache (LaCache). The idea is to keep earlier tokens in the sequence in the lower layer and the later tokens in the deeper layer, which intuitively makes sense.
Claims And Evidence: Experiments are conducted on the language modeling task (Wikitext and PG19) and tasks from LongBench for Llama-2-7B and Llama-3-8B. Results show that LaCache performs better than StreamingLLM on both tasks. However, I think the experiment is a little light and can be strengthened with more recent long-context models (see section on "Experimental Designs Or Analyses") and more baselines (see section on "Essential References Not Discussed").
Methods And Evaluation Criteria: The benchmark datasets (PG19 and Longbench) make sense.
Theoretical Claims: N/A
Experimental Designs Or Analyses: The paper primarily evaluated short context models (Llama-2-7B and Llama-3.1-8B) with up to 8K context length. These models inherently do not perform well on LongBench as most tasks have input exceeding the context length (e.g. for the PassageRetrieval task). As the proposed method aims to compress KV cache, it will be more suitable for evaluate on long-context models that can take longer input (e.g. Llama-3.1 and Qwen-2 models).
Supplementary Material: N/A
Relation To Broader Scientific Literature: This work contributes to the line of research on memory efficiency of long-context inference through KV cache compression, which is an active research area.
Essential References Not Discussed: Missing citation and related work:
* [SnapKV](https://arxiv.org/abs/2404.14469) (NeurIIPS 2024) is a relevant method which compresses KV cache based on input tokens' attention pattern, which is a stronger and more up-to-date baseline compared to H2O and StreamingLLM.
* [PyradmicInfer](https://aclanthology.org/2024.findings-acl.195.pdf) (ACL 2024) also proposes a layer specific KV cache eviction-based method and is a relevant baseline.
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: * Clarity of the proposed method: While figure 2 and figure 4 illustrate the procedure for LaCache, it would be helpful to include a pseudocode or algorithm to formally describe how the algorithm works.
Questions For Authors: * While it is not mentioned in the paper, I assume the compression happens at decoding time -- i.e. the model encodes the entire input for LongBench and perform LaCache compression. Is the understanding correct?
* What are the $S$ and $O$ used in the experiments of language modeling and LongBench experiments and how are they decided?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: Thank you for your time and constructive suggestions! We have addressed all your comments and suggestions as follows.
---
**Q1. Experiments on longer-context models trained on longer inputs**
Thank you for the suggestion! We have added experiments using both Llama3.2-3B-Instruct-128k and LongChat-7b-v1.5-32k to verify the consistent effectiveness of LaCache.
On the Needle In A Haystack (NIAH) benchmark, we evaluated both Llama3.2-3B-Instruct-128k (in [figure https://ibb.co/1GjhX0b5](https://ibb.co/1GjhX0b5)) and LongChat-7b-v1.5-32k (in [figure https://ibb.co/s9qp1s2K](https://ibb.co/s9qp1s2K)) under 50% and 25% cache budget settings. Our results demonstrate that LaCache nearly doubles the test accuracy compared to StreamingLLM under the same cache budget—for example, from 54.54% to 99.16% on the Llama3.2-3B-Instruct-128k model under a 50% cache budget, and from 33.40% to 65.30% on the LongChat-7b-v1.5-32k model under a 25% cache budget.
---
**Q2. Add more KV cache compression baselines**
Following your suggestions, we have added comparisons with both SnapKV [1] and PyramidInfer [2] as shown in [figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ). This set of results consistently validates that LaCache achieves better score-throughput trade-offs across various tasks on the LongBench benchmark.
---
**Q3. LaCache implementation and pseudocode**
Thank you for the constructive suggestion! We will include a more comprehensive version along with additional implementation details in our final manuscript.
---
**Q4. When LaCache is applied**
Yes, you are correct - it is applied at every step of decoding. Specifically, after prefilling the entire input, LaCache is used to reduce the KV cache and maintain it at a constant size by applying LaCache after each decoding step.
---
**Q5. Clarifications on the hyperparameters S and O**
The definitions of S and O are introduced at the end of Section 3.2 in our submitted manuscript.
(a) In long-context understanding tasks such as LongBench, S is set as an integer approximately equal to the number of layers multiplied by the overall compression ratio, aiming for a uniform compression ratio distribution. For example, under a 50% cache budget, setting the span equal to half the number of model layers results in a ~50% compression ratio across different positions, helping to avoid situations where some locations are over-compressed while others are under-compressed. In language modeling tasks, S is set to 1/4 of the number of model layers, which was given by the empirical results from our ablation studies, as shown in Figure 8.
(b) The choice of O depends on the task type. Specifically, a larger overlap (O) allows the information of a single token to be distributed across more positions, which is better suited for tasks requiring complex semantic understanding and greater global context. In contrast, a small overlap concentrates the information in fewer positions, which is more appropriate for tasks where the answers appear in a very narrow window.
| | Overlap=0 | Overlap=Span/4 | Overlap=Span/2 | $\Delta$ (Span/4 - 0) | $\Delta$ (Span/2 - 0) |
|-----------------|------------|------------------|------------------|----------------------|----------------------|
| QA tasks | 19.48 | 18.94 | 18.48 | -0.54 | -1.00 |
| Synthetic tasks | 5.17 | 5.67 | 6.17 | +0.50 | +1.00 |
For language modeling tasks, S is set to 1/2 of Span because of better semantic continuity. For long-context understanding tasks, following your suggestion, we have added above experiments on LongBench to demonstrate the impact of the overlap parameter O. As shown in the table, a larger overlap consistently improves performance on tasks that require more global information, such as synthetic tasks (PassageCount, PassageRetrieval-en, and PassageRetrieval-zh), while reducing performance on tasks that rely more on local information, such as QA tasks (NarrativeQA, Qasper, MultiFieldQA-en, and MultiFieldQA-zh).
---
**Q6. Missing citations and related work**
Thank you for pointing this out! We have added experiments on these two baselines as shown in [figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ) and will include these two related works in our final manuscript.
---
Thank you for your thoughtful suggestions that aim to help strengthen this paper! If you have any further questions or updated comments, we would really appreciate it and be happy to address them.
---
**References**
[1] SnapKV: LLM Knows What You are Looking for Before Generation
[2] PyramidInfer: Pyramid KV Cache Compression for High-throughput LLM Inference | Summary: * Paper proposed a training-free KV Cache compression which stores KV pairs not only sequentially (left-to-right within
each layer) but also across layers (from shallow to deep), giving deeper capabilities to capture long-range dependencies.
* Proposes iterative compaction mechanism that progressively compresses older caches, freeing up space for new tokens within a fixed cache size.
Claims And Evidence: * Different layers can maintain the KV Cache corresponding to different sets of tokens. This is a good insight.
* The ladder-shaped method is both intuitive to follow and well-developed.
* Iterative method to remove old KV Cache states to ensure memory compaction is a good idea.
* Figure 4 is useful visualization of the compaction technqiue.
Methods And Evaluation Criteria: * Experiments are carried out on standard long context benchmarks (LongBench) and LaCache shows very promising results.
* Comparison against both training-based methods (StreamingLLM) and training-free methods (H20, TOVA) is very helpful.
* Evaluation has been carried out on timely set of models
Theoretical Claims: None
Experimental Designs Or Analyses: * "Continuously extending a repetitive pattern and assigning coverage to each layer as equally as possible, which is ensured by our ladder-shaped pattern, improves the lower bound of the above minimax optimality than an unequal coverage strategy." This is a good insight.
* "An ever-expanding ladder pattern with partial overlaps creates a smoother fade-out of older tokens, helping to maintain stable information retention", also shows a deeper understanding of the problem.
* The ablation studies section is a little weak, considering only two hyperparameters. It is not clear yet if the parameters are both necessary and complete?
Supplementary Material: No supplementary material.
Relation To Broader Scientific Literature: * Both contributions presented are extremely relevant for practical LLM inference systems, the ladder-based compression and the memory compaction, both seem extremely practical.
Essential References Not Discussed: All references are discussed and most relevant works have been used appropriately as baselines.
Other Strengths And Weaknesses: * The effort for building LaCache's practical considerations is very helpful as it could be deployed easily with existing systems. Great to see the compatibility with systems such as Flash Attention. Very promising work.
Other Comments Or Suggestions: N/A
Questions For Authors: Minor concern: It is not clear if span and overlap are the only parameters which should be considered in the ladder-based design. Would be useful to see some additional analysis on that. Overall, this paper was a very interesting read.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for recognizing the insightfulness and promising results of our work, as well as for the constructive suggestions! We have addressed all your comments and suggestions as follows.
---
**Q1. More ablation studies and analyses on hyperparameters**
Thank you for the suggestion! We highlight that the ladder pattern can be fully determined by the two hyperparameters: Span and Overlap (i.e., S and O in Section 3.2 of our manuscript).
(a) In long-context understanding tasks such as LongBench, S is set as an integer approximately equal to the number of layers multiplied by the overall compression ratio, aiming for a uniform compression ratio distribution. For example, under a 50% cache budget, setting the span equal to half the number of model layers results in a ~50% compression ratio across different positions, helping to avoid situations where some locations are over-compressed while others are under-compressed. In language modeling tasks, S is set to 1/4 of the number of model layers, which was given by the empirical results from our ablation studies, as shown in Figure 8.
(b) The choice of O depends on the task type. Specifically, a larger overlap (O) allows the information of a single token to be distributed across more positions, which is better suited for tasks requiring complex semantic understanding and greater global context. In contrast, a small overlap concentrates the information in fewer positions, which is more appropriate for tasks where the answers appear in a very narrow window.
| | Overlap=0 | Overlap=Span/4 | Overlap=Span/2 | $\Delta$ (Span/4 - 0) | $\Delta$ (Span/2 - 0) |
|-----------------|------------|------------------|------------------|----------------------|----------------------|
| QA tasks | 19.48 | 18.94 | 18.48 | -0.54 | -1.00 |
| Synthetic tasks | 5.17 | 5.67 | 6.17 | +0.50 | +1.00 |
For language modeling tasks, S is set to 1/2 of Span because of better semantic continuity. For long-context understanding tasks, following your suggestion, we have added above experiments on LongBench to demonstrate the impact of the overlap parameter O. As shown in the table, a larger overlap consistently improves performance on tasks that require more global information, such as synthetic tasks (PassageCount, PassageRetrieval-en, and PassageRetrieval-zh), while reducing performance on tasks that rely more on local information, such as QA tasks (NarrativeQA, Qasper, MultiFieldQA-en, and MultiFieldQA-zh).
---
Thank you for your thoughtful suggestions to help strengthen this paper! If you have any further questions or updated comments, we would really appreciate it and be happy to address them. | Summary: The paper introduces LaCache, a scheme for progressive cache eviction for more efficient long context processing. Rather than evicting the same tokens at each layer, LaCache evicts tokens using a ladder-like scheme so that earlier layers maintain tokens from earlier in the context and later layers retain tokens from later in the context (with the immediate local context being fully preserved). They show that this scheme reduces the performance degradation from cache eviction and is more efficient than attention-based patterns for cache eviction; the size of each ladder "rung" and the overlap between rungs across layers are hyperparameters, which are analyzed in the analysis.
Claims And Evidence: Yes; the paper demonstrates the strong performance relative to reasonable baselines in terms of both downstream metrics and latency, compared with a fixed storage (KV cache size) budget.
Methods And Evaluation Criteria: Yes; I think the use of perplexity alone would not be convincing, so I appreciate the use of a diverse set of tasks from LongBench. It would be nice to show a non-perplexity task in the very long (>>16k) context regime; however, I understand there are not all that many tasks that fit this description.
Theoretical Claims: Not exactly a proof, more an informal optimization argument-- but I'm not fully convinced by the argument about the costs of compression patterns. In particular, since we are not working with tokens, but with contextual embeddings, it seems that some information about the "important tokens" will be present even if the embeddings of those tokens are not chosen; in addition, I'm not convinced that you can choose an ideal set of "important tokens" to maximize performance in the first place. This is not central to the paper, so it wasn't a major factor in my score; however, I don't think this section adds much to the argument.
Experimental Designs Or Analyses: Yes; I think the experimental design is reasonable and compared against good baselines.
I do think it would be nice to see results on the baselines other than StreamingLLM in the main table, especially as it seems that H2O might sometimes outperform StreamingLLM in downstream performance if not in latency.
Supplementary Material: N/A
Relation To Broader Scientific Literature: This is a crowded space, but I think this is a nice contribution and argues its point well. This is a type of fixed pattern I haven't seen before-- most methods evict the same tokens across layers, or use an attention-based decision at each layer. Using earlier layers for earlier tokens is an interesting idea.
Essential References Not Discussed: Not that I am aware of.
Other Strengths And Weaknesses: I particularly like the analysis described by Figure 3, where the caching pattern is compared to randomly chosen caching patterns across cache sizes. I think this is a nice extra that makes a strong argument for this technique.
Other Comments Or Suggestions: N/A
Questions For Authors: Q1. Can you report how LaCache compares to H2O on the remainder of the LongBench tasks you use?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for recognizing the contributions and analysis offered by our work, as well as for the constructive suggestions! We have addressed all your comments and suggestions as follows.
---
**Q1. Experiments on non-perplexity tasks with a long context regime (>>16k)**
Following your suggestions, we have added new experiments with context lengths up to 128k on both Llama3.2-3B-Instruct-128k and LongChat-7b-v1.5-32k to verify the consistent effectiveness of LaCache.
(a) On the Needle In A Haystack (NIAH) benchmark, we evaluated both Llama3.2-3B-Instruct-128k (in [figure https://ibb.co/1GjhX0b5](https://ibb.co/1GjhX0b5)) and LongChat-7b-v1.5-32k (in [figure https://ibb.co/s9qp1s2K](https://ibb.co/s9qp1s2K)) under both 50% and 25% cache budget settings. Our results demonstrate that LaCache nearly doubles the test accuracy compared to StreamingLLM under the same cache budget—for example, from 54.54% to 99.16% on the Llama3.2-3B-Instruct-128k model under a 50% cache budget, and from 33.40% to 65.30% on the LongChat-7b-v1.5-32k model under a 25% cache budget.
| Task | StreamingLLM | LaCache |
|--------------------|--------------|---------|
| niah_single_1 | 45.0 | 57.0 |
| niah_single_2 | 49.0 | 43.0 |
| niah_single_3 | 45.0 | 26.0 |
| niah_multikey_1 | 53.0 | 52.0 |
| niah_multikey_2 | 50.0 | 64.0 |
| niah_multikey_3 | 45.0 | 31.0 |
| niah_multivalue | 47.0 | 62.75 |
| niah_multiquery | 42.0 | 50.25 |
| vt | 29.4 | 60.8 |
| cwe | 17.2 | 61.0 |
| fwe | 42.0 | 45.67 |
| qa_1 | 75.0 | 67.0 |
| qa_2 | 43.0 | 41.0 |
| **Mean** | **44.82** | **50.88** |
(b) Similarly, on the RULER benchmark, we evaluated the LongChat-7b-v1.5-32k model under a 50% cache setting. The experimental results above verify the advantageous performance of LaCache under the same KV cache. Specifically, LaCache achieves a 5.06% higher average accuracy across 13 different tasks, especially in task cwe and fwe, where LaCache outperforms the baseline by a large margin.
---
**Q2. More analysis on the costs of compression patterns**
Thank you for your insightful comments! We agree that selecting an ideal set of "important tokens" to maximize performance is not the primary goal of our method.
The key point we aim to convey in this analysis is that LaCache improves over baselines by leveraging the insight that it is not necessary to maintain the same set of KV tokens across all layers. In particular, LaCache alleviates this redundancy through the proposed ladder pattern, which can more effectively cover potentially important tokens within a given budget and thus improve the lower bound of information retention. We will incorporate your suggestion and clarify this more clearly in the final version.
---
**Q3. Add more baselines on LongBench**
Thank you for your suggestion! We have added benchmarks with recent baselines, including both SnapKV [1] and PyramidInfer [2], as shown in [figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ). This set of results consistently validates that our LaCache achieves better score-throughput trade-offs across various tasks on the LongBench benchmark.
---
**Q4. Benchmark LaCache with H2O on the remainder of the LongBench tasks**
Following your suggestion, we have updated the overall performance comparison between LaCache and H2O on the entire 21 tasks of the LongBench benchmark as shown in [figure https://ibb.co/q3GrqCZQ](https://ibb.co/q3GrqCZQ), which demonstrates that LaCache achieves better F1-score-throughput trade-offs across various tasks on the full LongBench benchmark. We will also report results by categories in the final version.
---
Thank you for your thoughtful suggestions to help strengthen this paper! If you have any further questions or updated comments, we would really appreciate it and be happy to address them.
---
**References**
[1] SnapKV: LLM Knows What You are Looking for Before Generation
[2] PyramidInfer: Pyramid KV Cache Compression for High-throughput LLM Inference | null | null | null | null | null | null |
A Theoretical Framework For Overfitting In Energy-based Modeling | Accept (poster) | Summary: This paper analyses the training dynamics of learning a multi-dimensional Gaussian distribution from data. The training dynamics considered here is a continuous time gradient ascent optimizing the maximum likelihood objective. Under some assumptions on the starting point of the learning dynamic, the authors use techniques from random matrix theory to study the effect of finite training samples on the learning. They use this analysis to study effect of regularization and early-stopping. The analysis is also extended to Ising type models with the learning done in the high temperature/mean-field setting.
Claims And Evidence: The claims made in the paper are not clearly supported by analysis. This does not give any theoretical framework to analyse the training of EBMs. The analysis only applies to gaussian fitting where the explicit training dynamic can be analyzed. The general case is much more involved with a non-convex optimization dynamic. Also, applying the proposed methodology to the visible Botlzmann machine case will just give results that are not very interesting. In that case, the mean-field approach fails in the low-temperature regime where interesting multi-modality of the model emerges.
Methods And Evaluation Criteria: The use of synthetic data is probelmatic. Fig 1, says that the synthetic model closely mimics the real data sets. This does not seem to be true. The range of eigenvalues is completely different. Also the $M \rightarrow \infty$ limit of the synthetic model shows non-smooth behavior. It is unclear, if the results of the synthetic data model actually closely mimic that of actual datasets. This can be addressed by numerical comparison of the training dynamics of both the cases.
Theoretical Claims: (See questions)
Experimental Designs Or Analyses: (see questions)
Supplementary Material: I did not review the supplementary material closely.
Relation To Broader Scientific Literature: The authors have not clarified how their work connects to existing literature in analyzing gradient descent for convex problems under stochastic noise. Also, for models on discrete variables there exists other works that show that the learning problem can be solved sample optimally using methods based on learning conditionals. (See questions)
Essential References Not Discussed: (see questions)
Other Strengths And Weaknesses: (see questions)
Other Comments Or Suggestions: > The paper can be improved if the initial claims are toned down. As mentioned before, the analysis here does not extend to general EBMs. If the authors think that practical training protocols for generals EBMs can be studied using the gaussian approximation, then they should support that claim strongly with numerical or theoretical evidence in the paper.
> The discrete model analysis has to be removed or reworked to a more useful approach analyzing algorithms like interaction screening [VMLC16] or logistic regression [WSD19]. The review by Nguyen et.al. [CZB17] cited in the paper is unfortunately outdated for the inverse ising problem and does not consider the substantial advances in developing efficient algorithms for this problem in the last 7-8 years.
[VMLC16] Vuffray, Marc, et al. "Interaction screening: Efficient and sample-optimal learning of Ising models." Advances in neural information processing systems 29 (2016).
[WSD19] Wu, Shanshan, Sujay Sanghavi, and Alexandros G. Dimakis. "Sparse logistic regression learns all discrete pairwise graphical models." Advances in Neural Information Processing Systems 32 (2019).
[CZB17] Nguyen, H. Chau, Riccardo Zecchina, and Johannes Berg. "Inverse statistical problems: from the inverse Ising problem to data science." Advances in Physics 66.3 (2017): 197-261.
Questions For Authors: > Could the authors explain here or add a note to the Supp. Mat. showing the intermediate steps on how Eq (5) is derived? There some clarity lacking here. For instance the LHS of the second equation should be for the inner product between d(v^\beta)/dt and v^\alpha.
> Do the authors assume that J(t) and C^M are aligned for all t in the training dynamic? If these are aligned at t= 0, does this imply alignment at all times?
> Is the overfitting reported in this case really a case of overfitting in the traditional sense? In my view, the hypothesis model is not over-parametrized here. The fact that the test metrics achieve their optimum at a different time than the training metric is just an artifact of the different noise instantiations in the test and train dataset. That is, they are literally different metrics whose difference decreases in infinite sample limit. This does not seem to be an example of a complex model essentially memorizing the training samples and then failing to generalize on the test dataset.
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Methods and evaluation criteria**
We answer this comment about the choice of the spectrum in the answer to Rev. MN9R.
**Relation To Broader Scientific Literature:** Our work is focusing on the full-batch case since it is the typical case for the BM since you only need to compute the covariance matrix once.. We will add a few comments on the effect of considering minibatches in our framework. The second point answered below.
**Other Comments Or Suggestions**
We refer to the general reply (posted on Reviewer SPJf's section) about extensions to general EBMs.
We are unsure why the Reviewer suggests removing or altering the purpose of the discrete-variable analysis. The aim of this section is to demonstrate that the main features and insights obtained from the GEBM analysis—particularly the interpretation of the early stopping point—also apply to the case of discrete variables, within an otherwise identical setup. In both cases, the analysis is carried out on the standard gradient ascent algorithm for the log-likelihood maximization, which is the most generic way to train EBMs of arbitrary complexity. We do not claim that the proposed "cleaning approach" is sample-optimal or superior to other existing methods in the specific case of the inverse Ising problem; for instance, we are not discussing any comparison with other training schemes (e.g. pseudo-likelihood maximization or the interaction screening method), nor comparison with other mean-field like techniques suited for the Ising-BM. However, we will incorporate a discussion of the suggested references in the revised manuscript, and we would be glad to refer to a more recent review if the Reviewer could kindly provide a reference.
**Questions for authors**
About the alignment of $J(t)$ with $C^M$ at $t=0$: yes the dynamics remains aligned for all time in that case. If the initial condition $\boldsymbol{J}(0) $ is aligned with $\boldsymbol{C}^{M}$, it means that the two matrices commute, namely $\left[\boldsymbol{C}^{M}, \boldsymbol{J}(0)\right]=0$. From here, any gradient ascent step will add a term proportional to $-\boldsymbol{C}^{M}+ \boldsymbol{J}^{-1}(t)$: since both terms commute with which keeps the two matrices commute with each other. Alternatively, by looking at Eq. 5 (right) one immediately sees that if the initial condition is aligned with the eigenvector basis of $\boldsymbol{C}^M$, then $c_{\alpha, \beta}=0$ and the two matrices remain aligned at all times.
Additional numerical details about the alignment of the eigenvectors at the first stage of the training are discussed in Appendix B; it could be interesting to have a characterization of this transient time, but we don't have it yet and should follow from the more general theory mentioned in the common answer, that we plan to only sketch in this paper.
**About overfitting:** We thank the Reviewer for this question, it is indeed a point that might be worth discussing in the core of the paper. Our interpretation is the following: In the context of GEBM the weak modes of the empirical covariance that are eventually learned by the model correspond to directions of variance poorly estimated by the data and lead to overestimated coupling eigenvalues. As noticed by the Reviewer we are in the under-parameterized regime in this
case even though the ratio #samples/#parameters ($=M/N^2$) is typically below 1 in our experiments
but what matters is the ratio $\rho = M/N$ which becomes critical when equal to one because the covariance matrix ceases then to be invertible at that point. Nevertheless, when approaching
the interpolation threshold from above ($\rho>1$) there is a departure of the test LL from the train LL
corresponding to overfitting in this proportional scaling limit. Then
when looking at the more general formulation mentioned above corresponding to a kernel regime of score matching, this appears as a special case where the regression factorizes into $N$ independent problems (once the coupling matrix is aligned with the covariance matrix), which leads to consider $M/N$ scaling instead as $=M/N^2$. If we now consider the kernel setting with general EBM, there is no such factorization in general and we recover the standard picture of overfitting with $\rho = M/P$ where $P$
is the number of parameters. The over-parameterized regime then corresponds to learning the weak modes of the Gram matrix of the score features, i.e. typically high frequency modes able to define a localized energy function on each sample point.
**On the derivation of Eq. 5** We will add the details of the derivation in the appendix. The derivation first consider the decomposition $J_{ij} = \sum_\alpha v_i^\alpha J_\alpha v_j^\alpha$ before projecting the gradient on this new basis. Then we identify the diagonal terms leading to the dynamics of the eigenvalues and the off-diagonal ones leading to rotations in the space of the eigenvectors. | Summary: The given paper provides a theoretical analyses of overfitting in Energy-based models. Particularly, the scope of the paper is restricted to the analyses of Gaussian Energy-based Model (GEBM), wherein the authors show that the maximum likelihood (ML) training dynamics of GEBM is decomposed into different timescales. Specifically, the dominant mode features (corresponding to higher eigenvalue) are learnt early on whereas non-dominant mode features (corresponding to lower eigenvalue) are learnt later on during training.
The provided analyses shows that for finite number of training samples, the test log-likelihood (LL) improves upto certain time and then starts deteriorating. The authors provide analytical expression for this optimal stopping time ($t_{opt}$) using methods from RMT. Furthermore, the authors also provide several other results on optimal scaling factor, etc using RMT for a regularized training of GEBM. The authors conclude that overfitting observed in GEBM is mainly caused by the variation/noise in non-dominant modes in finite training sample setting, while this problem can be solved exactly when one has access to true model parameters. To this end, the authors propose to overcome the phenomenon of overfitting by using RMT to predict true model parameter via asymptotic results. However, most of the proposed solutions rely on quantities that rely on true model parameters. Lastly, the authors propose to fit a linear model to learn the eigenvalues of the data covariance, then use the model to extrapolate and use the extrapolated eigenvalues to determine the quantities of interest and avoid overfitting in finite sample cases.
Claims And Evidence: The authors have provided empirical and experimental proofs for most of their claims. However, I would like to see the following results as well:
1. Can you provide a plots of $\{c_\alpha^m\}$ against different $m$ so that one can verify that a linear fit would be good for extrapolation?
2. A similar plot for the Boltzman Machine learning would be helpful.
Methods And Evaluation Criteria: **Method**: The authors haven't provided any new method as such. Rather they give a rigorous theoretical insights into overfitting of EBMs (although this is limited to GEBM).
**Evaluation**: I understand that the provided analyses is limited to GEBM. However, the authors have shown spectral density on several datasets such as MNIST and CIFAR10. In that case, can the authors comment on how does their analyses apply to these datasets?
Theoretical Claims: I checked the theoretical correctness of the provided proofs and I cannot find any obvious mistake. However, I might have missed any tricky mistake as I am not well versed with RMT.
Experimental Designs Or Analyses: 1. The authors show spectral density of complex datasets like MNIST and CIFAR10, however, they don't show visual results of sampled datapoints obtained after training.
2. The authors should sample datapoints from MNIST and datasets mentioned in Fig. 7. Then compare how well these sampled datapoints are with few baselines like IGEBM (Du & Mordatch, 2019).
3. One should use Negative log-likelihood (NLL) and FID for the above comparison.
Supplementary Material: I have reviewed Supplementary materials except Section D.1.
Relation To Broader Scientific Literature: N/A
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: #### Strengths
1. The paper is fairly well written and presented.
2. To my knowledge, this is one of the first work that discusses the phenomenon of overfitting in EBMs. However, the scope of the provided analyses is limited to GEBM.
3. The conclusion drawn from the paper seems fair: the training dynamics first learns the dominant modes (which should correspond to low-frequency components) and then learns non-dominant modes (which should correspond to high-frequency components). This is in line with empirical observations as well.
#### Weaknesses
1. The paper seems weak empirically/experiment-wise. Although the paper provides a 'theoretical framework', the claims need to be verified on real world datasets.
2. The authors should show the result of sampling after training the model to verify the correctness of the method. E.g., a visual example of samples obtained using overfitted model against samples obtained using regularized model.
3. Identification of few key quantities like - $\lambda_{opt}$, $t_{opt}$ are not feasible since the true model parameters are unknown in practice.
4. The scope of the proposed analyses is limited to GEBM. However, somehow the observations are consistent with non-GEBMs like BM and datasets like CIFAR10.
Other Comments Or Suggestions: 1. Line 40, second col: generative -> generative modelling
2. Line 316, second col: circunvent -> circumvent
3. Line 373, second col: ~~Ref~~
4. Line 396, second col: exit -> exist
Questions For Authors: 1. $\hat{C}$ has been defined two times - after Eq. 1 and after Eq. 7. Are both the definitions same due to LLN?
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: **Claims and evidence:**
We thank the Reviewer for the suggestion, we will put in the appendix additional plots highlighting the behavior in $m$ of the down-sampled eigenvalues for both the GEBM and the BM.
**Methods and evaluation criteria:**
The eigenvalue spectra of the covariance matrices of real datasets as MNIST/CIFAR10 is depicted to guide us in a specific choice of a functional form of a a continuous spectral density used to derive the asymptotic results through RMT. The analysis on the GEBM can however be done using directly the eigenvalue spectrum of a real dataset. The only critical thing that should be considered is the addition of a threshold in the eigenvalues to avoid the existence of very small ones that would make the convergence extremely slow, and that have no effect on the timescales where the early stop point occurs. We will add some results on this regard in the appendix (see also last reply to Reviewer SJPf).
**Experimental Designs Or Analyses:**
We would like to stress that the experiments on real datasets are not very meaningful here, as the only thing that matters is their covariance matrix, i.e. the highest-order sufficient statistics of both the GEBM and BM. Our setting is not meant to reproduce with any level of quality samples from real datasets (e.g. MNIST/CIFAR10 images). In other terms, the GEBM is not used here to learn a "good" EBM to generate good-looking samples: that would be basically impossible because the GEBM only encodes for the first two moment statistics of the data with a single multivariate Gaussian, so that any sample generated according to the learnt GEBM would be far from a realistic image in the datasets cited above. The same holds for the BM: the binary BM does perform well as generative model, in the sense that it generates good Ising model samples, but this model, without hidden nodes, is known to perform very badly with images even at the level of MNIST dataset, as discussed e.g. in [Decelle et al, SciPost Physics, 2024], because high-order interactions are important.
The reason why we mention real datasets in the paper is to justify our choice of the synthetic spectrum but this procedure only looks at the eigenvalue spectrum of the real datasets' covariance matrix. Still, as mentioned in the reply to Reviewer MN9R, even such a reduced information about the spectral structure of real datasets is important to determine generalization properties even in deep networks (Yang, Mao, Chaudhari, ICML 2022).
**Strengths and weaknesses**
In the manuscript, we discuss both GEBMs and BMs. For the latter, the analytical treatment is restricted to the high-temperature phase and remains approximate; nonetheless, we demonstrate that it successfully captures the qualitative behavior observed in real experiments. In particular, we show that early stopping effects in BMs are analogous to those identified in GEBMs, and that they can be mitigated by applying the same regularization recipe introduced in the GEBM setting.
The models considered in this work serve as a controlled playground to analyze overfitting in a highly tractable setting. As discussed in our general response, we believe that the insights obtained here can be extended to more complex and realistic setups; however, such generalizations require dedicated studies, which we plan to pursue in future work. Our current goal is to establish a solid theoretical foundation upon which these future developments can be built.
About point 2: as explained before it is not meaningful here to compare single generated samples as it would be with datasets of images, but we will compare e.g. the generation error (i.e. the error between the covariances of generated samples and the population one) or other distance measures sugggested by Reviewer MN9R in the regularized and the un-regularized case. As stressed in the paper, it is true that in the GEBM the most dominant contribution to the error in the coupling matrix comes from the weak PCA directions, which are the least dominant in measures of generation quality, so we do not expect an improvement as net as in Fig.5(b).
**Questions For Authors**
This is correct: from Eq.1 the population covariance matrix is defined as the inverse of the GEBM's coupling matrix: that would also correspond to the empirical covariance matrix obtained computed with an infinite set of independent samples from Eq.1. | Summary: This paper proposes a theoretical framework for analyzing overfitting in energy-based models (EBMs). The framework is built upon two special cases of EBMs (namely, Gaussian EBM and Boltzmann Machine for inverse Ising model), which admit analytical (or partially/asymptotically analytical) solutions for the learning dynamics and stationary points (optimal solutions). This framework is later used to analyze the driving factors behind overfitting, suggest new overfitting mitigation strategies and reinterpret existing approaches.
It is claimed that the main reason behind the overfitting in the EGMs considered is the interplay between initialization and different learning timescales associated with eigendecomposition of the weight matrix. It is also claimed that the analysis provided is relevant to more complex models.
## update after rebuttal
During the rebuttal, most of my questions have been addressed.
The remaining are:
- Minor experimental analysis concern regarding the confidence intervals.
- Ablation on spectra lacks details (e.g., the expression used to define the spectra for Figure R2).
- I am still not convinced that one should mimic the spectral properties of the empirical datasets considered in the paper, because this data is of non-linear structure, and covariance matrix is a poor statistic to describe the properties of such datasets.
Although complex NN-based models are not directly targeted, the analysis is thorough and rigorous, which is a decent start. I have increased my score to 4. For more information, please refer to my last rebuttal reply.
Claims And Evidence: Overall, I find the claims related to GEBMs and BMs for the inverse Ising model to be well-supported by the theoretical and empirical evidence. The paper provided a comprehensive analysis of these models and corresponding overfitting mitigation strategies.
The only major claim I see problematic is the connection to non-toy-ish EBMs. Although the manuscript can provide some intuition regarding the general EBM case, the whole analysis revolves around spectral properties of the coupling/correlation matrices. The same goes for the protocols to mitigate overfitting. It is unclear how to extend these excellent results to a general, non-linear case.
Methods And Evaluation Criteria: I am mostly satisfied with the proposed method and evaluation criteria. However, there are several concerns which I would like to raise.
1. On lines 262-263 col.2 and in Figure 3, $\mathcal{E}_C = \Vert \hat{C} - C\Vert_F$ is referred to as "generation quality". However, to my knowledge, this quantity is not connected to any of the widely accepted divergencies used to assess the generation quality: neither $f$-divergencies [3a], nor Wasserstein distances [3b]. Perhaps, the authors should refer to $ \mathcal{E}_C $ as just "covariance matrix reconstruction error". I also suggest adding the closed-form expressions from [3a,3b] to track how well the learned $J$ reproduces the original distribution. This will enable overfitting analysis from the distribution matching perspective, which is more interesting in the context of generative learning. These additional metrics might also provide new information, thus complementing the analysis based on log-likelihood, energies and matrix errors.
2. I feel uncertain about using MNIST, CIFAR10, HGD and Ising 2D datasets for correlation matrix spectral analysis. These datasets are of highly non-linear structure, which makes me question the relevance of the spectra reported in Figures 1,7 for the research provided. It is unclear why one should try to reproduce the spectral properties of covariance matrices of datasets which are far from being Gaussian.
3. Still, taking Figures 1,7 into consideration, it is unclear why it was decided to introduce nonsmoothness at $x=1$ in (10). From FIgures 1,7 it is clear that real spectrum is smooth. Perhaps, the authors should provide additional experiments showing that the results (at least, the key results) are robust to the choice of the spectral density.
[3a] Frank Nielsen, Kazuki Okamura. "On the $f$-divergences between densities of a multivariate location or scale family". arXiv:2204.10952
[3b] Salmona et al. "Gromov-Wasserstein Distances between Gaussian Distributions". Journal of Applied Probability, 2022, 59 (4). hal-03197398v2
Theoretical Claims: I satisfied with the theoretical part of the work. I find the corresponding theoretical claims convincing and backed up with not only proofs, but also the experimental results. Below I provide my (mostly, minor) concerns regarding this part.
I can not follow the derivation on lines 93-109 col.2. Particularly, I am unable to reproduce the gradient provided in (3). My own calculations yield $ [-C^M_{ij} + (J^{-1})_{ij}] $. Additionally, if we assume $C^M=0$ (which, of course, does not correspond to any real case, but can be used for the sake of analysis), we should get $\partial L / \partial J{i j} = \partial \log\det J / \partial J{ij} = (J^{-1}){ij}$, which does not hold when using (3). Finally, in (4) the $\Lambda$ matrix seems to disappear. Please, clarify.
Experimental Designs Or Analyses: I have minor concerns regarding the experimental setups and analyses.
1. Perhaps, using several seeds and reporting mean values and error bounds in Figures 1,7 will be more convincing to the latter analysis (it is hard to verify the under-/overestimation observations judging by several samples only).
2. From the text, I understand that Figure 2 is provided to highlight the difference of $J_\alpha(t)$ dynamics when (a) ground-truth or (b) empirical covariance matrix is used. However, it is therefore unclear why different learning rate $\gamma$ was used.
Supplementary Material: I have superficially read the Appendix. The authors do not provide other supplementary material.
Relation To Broader Scientific Literature: I can not pinpoint any specific prior work that targets the problem of overfitting in EBMs.
Essential References Not Discussed: I can not recall any specific work which is essential for understanding the context of the submission and is not cited.
Other Strengths And Weaknesses: The paper is comprehensive, well-written and was enjoyable to read.
Other Comments Or Suggestions: I understand that the topic is deeply rooted in statistical mechanics. I also acknowledge the freedom of choosing the notation which is more convenient for the authors. Still, I find the latter to be a little confusing.
1. From my experience, in papers on machine learning or statistics, $\langle \dots \rangle$ is rarely used to denote expectation; rather, it can be used for empirical averaging, whereas the expectation is denoted by $\mathbb{E}$.
2. Additionally, denoting the ground-truth covariance matrix by $\hat{C}$ and the empirical estimate by $C^M$ is also very unusual. It is usually expected that `\hat` is used for estimates, and no accent marks are used for the ground-truth values.
Typos:
1. Lines 57, 60 col.1: inconsistent usage of spaces before and after "—".
1. Similar for lines 636-638.
1. Lines 74-75 col.2: "-" is used instead of "—".
1. Line 101 col.2: "the gradient of (2)" - perhaps, "the gradient in (2)" (as it is the gradient of $\mathcal{L}$) was intended.
Questions For Authors: 1. How the framework proposed can be extended to complex EBMs?
2. Have you tried other spectral densities instead of (10)?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: **Methods and evaluation**
1. It is true that the choice of the generation quality measure with the Frobenius norm does not reflect a measure of distance between two probability distributions in general, but it is inspired by real experiments where actually such a metric is widely used, for instance in inverse Ising/Potts approaches in order to compare e.g. correlations matrices between the original dataset and generated configurations. In the GEBM it is also true that the metrics suggested by the Reviewer is a better measure of discrepancy between distributions. We have computed in particular the Wasserstein distance between the true GEBM and the inferred one along the training dynamics: also this quantity turns out to display a non-monotonic behavior w.r.t. the training time, and moreover the optimal time computed using this metric seems to be the closest one to the optimal time obtained by maximizing the test-LL. We will discuss these other measures in the final version of the manuscript.
2. **Choice of the spectrum.** For the GEBM analysis, we do not employ real datasets directly. Instead, we construct synthetic covariance matrices designed to mimic the spectral properties typically observed in empirical data, with the aim of explaining early stopping effects reported in real experiments. Specifically, we chose a synthetic spectrum with two distinct branches to visually and analytically distinguish between dominant (strong) and subdominant (weak) modes in the population covariance matrix. We would like to emphasize that this two regimes spectral structure is supported by previous works identifying similar two-regime behavior in real datasets (see, e.g., [Yang, R. et al., ICML 2022)]. In the final version of the manuscript we will display the real and synthetic eigenvalue spectra in log-log scale where this common trait can be more easily visualized. That said, the theoretical framework we develop does not rely on the specific details of the eigenvalue spectrum, provided the population covariance matrix is non-degenerate. We tested a variety of synthetic spectra and observed no qualitative differences in the results. For example, modifying the parameters in Eq.~(10) leads to the same learning dynamics as discussed in the manuscript.
The choice of synthetic spectrum is guided by numerical constraints: the RMT equations require discretization of the spectral density, and very small eigenvalues significantly increase computational cost due to the need for extremely fine resolution in the integration.
We understand the concern and will include a dedicated appendix in the revised version of the manuscript to explicitly illustrate the robustness of our results with respect to changes in the eigenvalue spectrum.
**Theoretical claims**
The presence/absence of the term $\Lambda_{ij}$ arises whether one assumes that the perturbation of the log-likelihood w.r.t. to one interaction $J_{ij}$ to be symmetric or not. Of course this holds only when $i\neq j$, that is why the term $\Lambda_{ij}$ appears.
It is actually true that in the following steps of the derivation we did not use this additional term when projecting the gradient, nor in the numerical gradient ascent procedure: this is basically equivalent to assume that perturbations instead are non-symmetric ( a more detailed discussion about the two different ways of taking likelihood's derivatives is given e.g. in [Magnus, J. R., Neudecker, H. (1999)]). A practical solution to this problem is to absorb it in the learning rate, meaning that the diagonal terms $J_{ij}$ will evolve in time with a learning rate doubled w.r.t. to the off-diagonal terms to compensate that factor.
**Experimental Designs Or Analyses**
1. About the mean values on Figures 1,7: both figures show the mean eigenvalue spectra of the empirical covariance matrix of a dataset at a given number of samples $M$: here the average is intended w.r.t. a certain number $n$ of different downsampling of $M$ samples from the original full dataset with $M^*$ samples. We have chosen a large enough $n$ (specifically $n=1000$) such that the standard error of any mean eigenvalue is not appreciable in the plot's scale. Having said this, we will add errorbars or shadows to the figure to highlight the standard deviation between realizations, reduce $n$ in order to have disjoint subset of samples to compute the covariance matrix.
2. This is correct. In the left panel, we wish to compare the theoretical behavior (continuous time limit) with the one obtain by maximizing the likelihood using GD. The continuous limit is correct for very small learning rate, which is why $\gamma$ is very small. On the right panel, we only consider the resolution of the evolution equations, hence the learning rate didn't matter here as it only renormalize the time.
**Relevance for more complex non-linear models** See the common answer written in the rebuttal of rev. SJPf.
---
Rebuttal Comment 1.1:
Comment: I would like to thank the authors for their thorough response.
I would appreciate it if you could upload the plots and other materials referenced in your reply using an anonymous service (e.g., 4open.science), so that I and the other reviewers can get acquainted with the additional results. After that, I will be able to fully assess the response.
**Updated response after the additional materials have been provided**
Thank you for providing supplementary results and clarifications. The work is now more appealing to me. Although complex NN-based models are not targeted, the analysis is thorough and rigorous, which is a decent start.
Below I also list my (minor) remaining concerns, which I hope to be addressed in the next revision:
- It seems that the confidence intervals are plotted for mean values, which explains their size. However, perhaps, standard deviation for the eigenvalues themselves should be plotted (not for the mean value) to better illustrate the variance of individual observations.
- Please, provide more details for the ablation on spectra (e.g., the expression used to define the spectra for Figure R2).
- I am still not convinced that one should mimic the spectral properties of the empirical datasets considered in the paper, because this data is of non-linear structure, and covariance matrix is a poor statistic to describe the properties of such datasets. Perhaps, more effort should be put into finding real data admitting linear or close-to-linear structure?
I will increase my score.
---
Reply to Comment 1.1.1:
Comment: We have have created an anonymous repository that includes a .pdf file with the requested plots:
https://anonymous.4open.science/r/ICML_reply-6020/ReplyMN9R.pdf
**Additional reply**
In the following link we have added another .pdf file with additional details about first answer to
"1. Common reply about model relevance and applicability to more complex EBMs":
https://anonymous.4open.science/r/ICML_reply-CB48/ | Summary: The authors present an analysis of training dynamics and overfitting in different settings (infinite data, limited data, continuous domain, binary domain) for a specific class of EBMs. The basic idea is to project the training dynamics to the principal components of the coupling matrix, which allows (in the class of models the authors study) for strong analytic claims.The authors also study common methods for mitigating overfitting (like regularization) in their framework.
UPDATE AFTER REBUTTAL:
The paper is limited in that they are studying GEBM, which limits its immediate applicability, but the work is nonetheless interesting, novel and thoroughly conducted. The authors also addressed my concerns. I therefore change my rating to 'accept'.
Claims And Evidence: The claims are very well supported: The authors base them on theoretical analysis and show excellent agreement with experiment. The projection of the training dynamics into eigenspace is well done and interesting.
Methods And Evaluation Criteria: The methods and evaluation criteria show quite exactly what the authors want to show. However, in order for the paper to be relevant for the wider field the evaluations are not sufficient: The experiments are small scale and the data very far from what ML methods are typically applied to. It is not clear how this analysis would work in more realistic scenario.
Theoretical Claims: I did not do the math but it seems to be relatively straight-forward and the results are sensible.
Experimental Designs Or Analyses: I am quite confident that the experiments are valid. They coincide with the theoretical predictions and the setting is relatively small-scale and controlled.
Supplementary Material: No.
Relation To Broader Scientific Literature: The relate to random matrix theory and inverse Ising problems. The paper is well-embedded in this field.
Essential References Not Discussed: Not that I know of, but some of the topics touched have a vast literature spanning several decades, so I am not entirely sure.
Other Strengths And Weaknesses: Strengths:
1) Setup & Execution: The paper is beautifully written and the analysis is clean and done well, the visualization and experiments are convincing
2) Novel results: The results are non-trivial and the agreement with experiment is very good
3) Interesting to some groups: The paper is very interesting to anyone working in the field of statistical methods applied to ML (and related fields like inverse Ising/Potts etc.). However (read below under "weaknesses"), these groups do not correspond to the core audience of ICML.
Weakness:
1) Model relevance: The type of models analyzed are toy models at best. I am not aware of anyone using these kind of models in moden ML (please correct me if I'm wrong). The most relevant case I know of where this analysis might apply are inverse methods applied to protein sequences, but even that seems to have been largely abandoned. The applied papers that the authors cite are either old or quite niche.
2) Data relevance: The authors use either synthetic data or MNIST.
I think the paper is worth publishing if the authors argue that their analysis could be extended to a more realistic setting. I am quite confident that if pursued consistently this type of analysis could be valuable for the wider community.
Other Comments Or Suggestions: Very minor: It's "Frobenius", without the umlaut.
Questions For Authors: Could you argue that this type of analysis could be extended to more realistic settings? For now my rating is "Weak Accept" but I am happy to increase the rating if you can argue for this.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: ## **1. Common reply about model relevance and applicability to more complex EBMs**
We thank all the reviewers for their comments.
All Reviewers have raised important concerns regarding the generality of the results presented in the paper, particularly their applicability to more complex or realistic generative models. While we fully acknowledge that our analysis is far from the architectures typically employed in contemporary machine learning, we would like to emphasize that, to the best of our knowledge, this is the first work to tackle the problem of overfitting in energy based generative models. To start with something concrete and tractable we consider here Gaussian multivariate models which might indeed look over-simplistic and irrelevant regarding modern ML. The logic here is a bit similar as the one considering linear regression for understanding deep learning [Belkin2018,Hastie2022]. Actually we found a concrete parallel to that and **plan to add a new section in the main-text and supplementary material discussing it in detail**. The argument goes as follows: if we consider score-matching [Hyvarinen2005] as a proxy for studying theoretically the learning of EBMs, we arrive at a description of the learning dynamics in terms of a neural tangent kernel dynamics [Jacot2018] of the score function ($\psi(x,\theta) =-\nabla_x E(x,\theta)$, i.e. the gradient of the energy function of the EBM) of the form
$$
\frac{d\psi(x\vert\theta_t)}{dt} = -\hat{\mathbb E}_{x'}\Bigl[K_t(x,x')\psi(x'\vert\theta_t)\Bigr] + \hat \phi_t(x)
$$
where the kernel $K$ and the source $\hat\phi$ is build on a tangent space corresponding to the derivative of the score function w.r.t the parameters. Considering then the dynamics corresponding to a lazy training regime [Chizat2019] where the NTK (and also $\hat\phi$) can be assumed deterministic we end up with a similar dynamics as for Gaussian EBM, driven now by the empirical covariance matrix of score features instead of the input features. The empirical covariance matrix on the input feature is now replaced by a covariance of tangent score functions, which are as well expected to be in the random matrix regime and overfitting will as well occur when weak modes of this covariance starts to be learned. So in the end we have potentially a much broader theory, which encompasses exponential models and more generally the EBM in the kernel regime.
[Hastie2022] Hastie, Montanari, Rosset, Tibshirani Ann. of Stat. (2022)
[Hyvarinen2005] Hyvärinen, Dayan, JMLR (2005)
[Jacot2018] Jacot, Gabriel, Hongler, NeurIPS (2018)
[Shizat2019] Chizat, Oyallon, Bach, Neurips(2019)
## **2. Specific answer to the reviewer:**
**Methods and evaluation criteria:**
The experiments we have conducted on the GEBM, although performed at relatively small system sizes — with most results in the main text corresponding to $N = 100$ — exhibit excellent agreement with the asymptotic predictions derived from Random Matrix Theory (RMT). As shown in Fig.~4 (notably panels a and c), the empirical results obtained at $N = 100$ already display perfect overlap with the theoretical curves expected in the limit $N, M \to \infty$.
Regarding the Boltzmann Machine (BM), it is true that the system size employed ($N = 64$ spins) is smaller than what is typically used in standard machine learning applications. Nevertheless, the qualitative behavior we observe is robust with respect to system size. These BM experiments are intended to demonstrate that the key phenomenology observed in the GEBM carries over to the BM case. In particular, we highlight the emergence of negative eigenvalues in the coupling matrix and the role of finite-sampling noise, which primarily affects the learning dynamics associated with the smallest principal components of the data. To strengthen the robustness of these findings, we plan to perform additional numerical experiments at larger system sizes for the final version of the manuscript.
**Using real datasets --** Our results do not depend on the specific dataset used, as they are based on a given arbitrary covariance matrix, which can be derived from any dataset. The use of synthetic data is motivated by the need to control the asymptotic limit required for the Random Matrix Theory (RMT) analysis, and to ensure that the eigenvalues are not too small at this limit — a condition that would otherwise significantly increase the computational cost, since small eigenvalues necessitate extremely fine discretizations for solving the numerical RMT equations. Nevertheless, we can always consider a cutoff which should only have effects far away from the early stopping point.
In the final version of the paper, we will include an additional section in the Appendix where we reproduce the results using different eigenvalue spectra taken from real datasets and different parameters for the synthetic model, explicitly showing that the qualitative behavior remains unchanged. | null | null | null | null | null | null |
DriveGPT: Scaling Autoregressive Behavior Models for Driving | Accept (poster) | Summary: This paper explores behavior modeling for autonomous driving and investigates the scaling properties from data to model parameters. The proposed method, DriveGPT, validates the benefits of scaling up both training data and compute, demonstrating improved model scalability as data increases—consistent with findings in language model scaling. To assess effectiveness, quantitative and qualitative comparisons are conducted across models from the scaling experiments. Furthermore, real-world deployment is showcased through closed-loop driving in challenging conditions, demonstrating the model's generalizability on the Waymo Open Motion Dataset, where it outperforms previous state-of-the-art methods in motion prediction.
Claims And Evidence: This paper claims similar scaling properties in behavior modeling, supported by experiments. However, although scaling effects are observed in validation loss, the model's scaling effect is not significant. From Table 3, it appears that there is little improvement in performance beyond 94M.
Methods And Evaluation Criteria: This paper explores scaling properties using the same paradigm as LLMs. From the validation loss and the internal and WOMD evaluation metrics, the approach appears generally reasonable.
Theoretical Claims: No theoretical claims.
Experimental Designs Or Analyses: The overall analysis of the experiments is fairly thorough, with testing conducted on both internal experiments and WOMD. However, the results suggest that models around 100M perform the best. How do larger models perform? The scaling gains of the model appear to be not very significant, especially when compared to LLMs, where models with hundreds of millions of parameters are still considered relatively small.
Supplementary Material: The supplementary materials provide videos, which show good performance in behaviors such as unprotected left turns and lane changes. The appendix section includes more ablation experiments.
Relation To Broader Scientific Literature: This paper aims to advance research in behavior modeling for autonomous vehicles. Previous work has mainly explored small datasets and models, while this paper explores the effects of scaling in behavior modeling, which is highly valuable for the future development of autonomous driving.
Essential References Not Discussed: There is another line of methods, such as [1] and [2], that approach behavior modeling from an image modeling perspective and also use transformers for autoregressive action prediction. These methods can be briefly discussed in the related works section.
[1] DrivingGPT: Unifying Driving World Modeling and Planning with Multi-modal Autoregressive Transformers
[2] DrivingWorld: Constructing World Model for Autonomous Driving via Video GPT
Other Strengths And Weaknesses: 1. Is it possible to release some of the internal driving data in the future to facilitate further exploration?
Other Comments Or Suggestions: 1. Is the quality of the data also important, such as trajectory mining in complex scenarios, rather than just scaling the data volume?
Questions For Authors: 1. How is the validation set divided?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for your review and positive comments about our work. We are encouraged by your recognition of the value of our work for the future development of autonomous driving.
We address your comments and questions below.
---
**Larger models beyond 94M**
We agree with the reviewer’s observation that geometric metrics stabilize beyond 94M in Table 3, yet we have found that semantic metrics, such as collision rate, continue to improve as the model scales to 163M, as shown in the last column of Table 3 and further discussed in Section 5.1.2 (Page 7, Line 355). These results suggest that increasing model parameters could yield additional benefits in actual driving performance. In the final version, we will provide more qualitative comparisons between the 94M and 163M models in terms of semantic driving performance.
---
**Scaling gains compared to LLMs**
We appreciate the reviewer’s observation regarding the scale of our models compared to LLMs, which are typically trained on trillions of tokens with billions of parameters. A key challenge in scaling driving models is the collection of large-scale driving datasets. Unlike text data, which is abundant and easily accessible, high-quality driving data is expensive to acquire, requiring extensive real-world deployment across diverse scenarios. As discussed in Section 1 (Page 1, Line 043), this makes scaling driving models inherently more challenging than scaling LLMs.
Despite being relatively smaller in scale compared to LLMs, our work represents the largest effort in scaling driving behavior models to date. As reviewer *mYMk* noted, “Even though it seems the conclusion must be that magnitudes of more data and FLOPs leads soon to diminishing returns, that is an insight that is potentially very interesting for the community.” We hope our findings provide meaningful insights to the community and contribute to the advancement of the next generation of foundation models for autonomous driving.
---
**Image-based behavior modeling literature**
Thanks for highlighting these methods. We will include discussions on DrivingGPT and DrivingWorld in the related works section of the final version. As discussed in the paper, our approach focuses on a simple and scalable autoregressive model architecture, leveraging commonly adopted vector representations in the field. We believe our insights could be extended to additional input representations and encoders in future work.
---
**Data release**
We are highly interested in releasing a subset of our internal driving data and providing additional metadata information to facilitate further exploration in the field, which is currently pending internal review.
---
**Data quality**
We carefully curated our dataset to encompass a diverse range of urban driving scenarios with balanced distributions, including lane changes, intersections, double-parked vehicles, construction zones, and close interactions with pedestrians and cyclists. We believe that further improving data quality and sample diversity could enhance scaling results and defer a more comprehensive study as future work. We will add more details in the final version.
---
**Validation set**
The validation set was curated to include 10M samples sharing the same distribution as the training set but with no overlap. We used the same validation set for all scaling experiments for consistency. We will add clarifications in the final version.
---
Thank you once again for your time and thoughtful feedback. We hope that we have addressed your questions and that you will consider supporting the acceptance of our manuscript. | Summary: This paper presents DriveGPT, a scalable behavior model for autonomous driving. The model has 1.4B parameters and 120M data are trained. DriveGPT is ∼3x larger and is trained on ∼50x more data sequences than existing published behavior models.
Claims And Evidence: Yes.
Methods And Evaluation Criteria: Yes.
Theoretical Claims: NA.
Experimental Designs Or Analyses: Yes. Good experiment results of scaling law of motion prediction models.
Supplementary Material: Yes. The supplementary material contains qualitative results of planning trajectories of the ego-vehicle.
Relation To Broader Scientific Literature: Scaled up the model and dataset.
Essential References Not Discussed: Yes. I browsed the WOMD leaderboard and noticed that some of the top-performing methods haven't been discussed, like [A] and [B].
[A] MGTR: Multi-Granular Transformer for Motion Prediction with LiDAR
[B] ControlMTR: Control-Guided Motion Transformer with Scene-Compliant Intention Points for Feasible Motion Prediction
Other Strengths And Weaknesses: Strengths:
- The paper is well-written and easy to follow.
- This paper explores the scaling law of the motion prediction large models.
Weaknesses:
- The main concerns are in the experiments. (1) The motion prediction results on WOMD (Table 4) only include works before 2023. The shown methods are not leading-edge enough at present. (2) The results are much lower considering the Soft mAP metric. The authors claim this is "due to suboptimal probability estimates". However, I'm not familiar enough with this task to fully understand their explanation.
Other Comments Or Suggestions: NA.
Questions For Authors: Please refer to the concerns listed above, especilly for the comparisons with other methods.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for your time and feedback. We appreciate the positive assessment of our well-written paper, good experiment results, and contribution to exploring the scaling law of the motion prediction large models.
We address your comments and questions below.
---
**WOMD top-performing methods**
We appreciate the reviewer for highlighting these methods that achieve top performance on WOMD.
MGTR leverages an augmented WOMD-LiDAR dataset that incorporates additional LiDAR inputs, which are not available in the standard WOMD dataset used by our method and most existing baselines in the literature (e.g., MTR, Wayformer, MotionLM). While we adhere to the standard WOMD dataset and use the open-sourced MTR encoder implementations for better reproducibility, our approach does not make any specific assumptions about encoder design. We believe our insights could be extended to additional input modalities and encoders in future work.
ControlMTR introduces a set of novel techniques to improve upon MTR. As shown in Table 4 of our paper and Table II in ControlMTR [B], our method outperforms ControlMTR in terms of minADE, minFDE, and MR.
We will ensure that discussions on these two methods, as well as additional relevant papers from the WOMD leaderboard, are included in the final version.
---
**Table 4 baselines**
We appreciate the reviewer’s comments on our WOMD baselines. While most of our baselines were published in 2023, Wayformer remains a high-ranked method on the WOMD 2024 leaderboard among all published and preprint papers.
Among all 30 methods on the WOMD 2024 leaderboard (https://waymo.com/open/challenges/2024/motion-prediction/), our minADE of 0.5240 and minFDE of 1.0538 are the second best, trailing only IMPACT_e2e, which was submitted in March 2025 (after our paper submission) and has no publication or preprint record as of today.
In the final version, we will include results from recently published papers and preprints, including [A] and [B] as referenced by the reviewer.
---
**Soft mAP clarification**
We discussed our soft mAP results in Section 5.2.3 (Page 8, Line 416). This limitation arises from using an autoregressive decoder to estimate sample weights, which are computed by accumulating probability estimates at each prediction step, as shown in Eq. (1).
More specifically, in WOMD, the model predicts 80 steps into the future to generate 8-second trajectory samples. Summing log probabilities over these steps can introduce compounding noise, leading to suboptimal probability estimates for each sample and lower soft mAP scores, which depend on accurate probability estimates across predicted samples.
While we follow the standard approach from the LLM literature for computing autoregressive sample weights, a potential venue for future work is to train an additional probability prediction head for each sample, which could enhance probability estimates and lead to improved soft mAP scores. We will further clarify this limitation with additional details in the final version.
---
**Clarification of contribution**
As we intend to demonstrate the generalizability of our method through WOMD experiments, the primary contribution of this work lies in providing a unique perspective to the community through our empirical scaling results, as acknowledged by the reviewer (“This paper explores the scaling law of the motion prediction large models”) and other reviewers (Reviewer *mYMk*: “The architecture is actually very simple. For an investigation into scaling laws this is positive to make it easier to attribute any performance gains”; “scaling driving performance is hard to estimate without large computational resources and datasets, which the authors both provided... that is an insight that is potentially very interesting for the community”. Reviewer *i1gv*: “this paper explores the effects of scaling in behavior modeling, which is highly valuable for the future development of autonomous driving”).
We hope our findings offer insightful contributions to the community and inspire further research in this direction.
---
Thank you again for your valuable feedback. We hope our responses sufficiently address your concerns and clarify the contributions and impact of our work. We would greatly appreciate your support in allowing us to share what we believe are meaningful insights with a broader audience and contribute to the advancement of next-generation foundation models for autonomous driving. | Summary: The paper presents a large transformer model predicting future ego agent states in a Birds Eye View for autonomous driving. The focus lies on an investigation of the scaling properties of transformers for behavior modeling by increasing the model and dataset size significantly. The method beats some baselines on the Waymo Open Prediction test Dataset and can be transformed into a prediction planning method to drive in real life.
## update after rebuttal
Given the rebuttal of the authors and comments of other reviewers I do not see controversy in leaning towards acceptance. Therefore I leave my original rating.
Claims And Evidence: - Present DriveGPT (fulfilled with the paper)
- Determine empirical driving scaling laws for auto-regressive behavior models.
Detailed investigations with fixed or variable FLOP budgets, parameter and dataset sizes and comparison with baselines are given, e.g. in Figure 5 and 6.
- Validate in real-world scenarios and closed-loop driving
This is shown in one video and described in one small paragraph. While interesting this seems under-reported.
- Outperform SOTA on WOMD
The model seems to be among the best, with very good minADE and minFDE values. Miss rate and Soft mAP are better for other approaches which the authors report themselves.
Methods And Evaluation Criteria: The WOMD test set is used widely in the domain and is suitable for comparing marginal prediction as done with this model.
Theoretical Claims: Claims are empirical and not theoretical.
Experimental Designs Or Analyses: The method has a very simple straightforward design which is not hard to understand. The experimental design is common in the domain where approaches are compared on BEV views in terms of standardized metrics. There are no general issue apart from missing clarity of the closed-loop setting (more below).
Supplementary Material: The video suggests good performance in real driving.
Relation To Broader Scientific Literature: The paper beats the state of the art but does not really try to improve on a methodological level a specific architectural trick or additional input modalities. The work positions itself well within conservative standards regarding the method but then investigates scalability using resources which are not easily available to others. The contribution to the literature is therefore probably biggest in terms of the study on scalability.
Essential References Not Discussed: Some baselines are succeeded by newer approaches, e.g. MTR now competes in the Waymo challenge as MTR++. "MTR++: Multi-Agent Motion Prediction with Symmetric Scene Modeling and Guided Intention Querying", Shi et al. (2024 arXiv). However, while the approaches are compared on the Waymo leaderboard the relevant paper is not yet peer reviewed and published. So in this fast moving field there are some references not discussed but for this study it is probably justified to compare to the field at a decently recent point in time as the authors did.
Other Strengths And Weaknesses: Strengths:
The approach seems to assign a significant probability to alternative paths which is a good thing. Comparable approaches can suffer from mode collapse, predict only one solution and then struggle when the driving situation changes quickly or in an unexpected way. This is well illustrated in Figure 11.
The architecture is actually very simple. For an investigation into scaling laws this is positive to make it easier to attribute any performance gains.
The range of investigations, including those in the appendix, are interesting for the domain because they are hard to reproduce. Given the large training set and amount of GPUs used the contribution here lies also in providing a study that a group with less resources could not do.
Weaknesses:
Results on the WOMD test set do show a better minADE and minFDE rate but do not outperform MotionLM Ensemble on the Miss Rate or Soft mAP. Given the high amount of parameters and training examples, this would suggest the approach leads to diminishing returns. This is further suggested by Table 8 in the appendix.
The performance can not be reproduced or built upon from the very limited information about the "Large-scale driving dataset". The least amount of information which would be needed would be countries in which the recording took place, percentage of rural vs. city driving, percentage of daytime vs. nighttime driving and ideally some information about the data recording. It was shown in "A Review and Comparative Study on Probabilistic Object Detection in Autonomous Driving" Feng et al. (ITSC 2020) that performance across datasets can vary a lot even if they were recorded in the same country. Without camera input that effect will be smaller. However, to maximize the usefulness of the insights of this study more information should be given to be able to judge the amount of outliers, proportion of cyclists and humans, their customs of crossing the street and other regional features that can impact some methods more than others.
In Figure 1, it is not clear what the smaller baseline is. Information should be given about the proportion of training data used and architecture. Is it the same transformer simply trained on less data? If yes, on how much less?
There should be more information about the closed-loop driving. Presumably the system drove on real streets with a safety driver but is DriveGPT really used to drive the car? Detection of traffic lights, complex local rules which are potentially only in place during certain hours and ad-hoc instructions by traffic guiding police officers would be surely an issue. It is not clear which of the models was used on the street as well. Training happened on 16 H100 GPUs, how was driving realized? If inference needs the same amount of compute, was that realized in a car or remote? If in a car, was there some distillation involved? The information about this contribution are lacking a lot of details.
In summary, the paper seems to shows a moderately better performance, beating the state of the art incrementally. While there is no large methodological novelty the study is a valuable investigation. In parallel to scaling large language models, scaling driving performance is hard to estimate without large computational resources and datasets, which the authors both provided. Even though it seems the conclusion must be that magnitudes of more data and FLOPs leads soon to diminishing returns, that is an insight that is potentially very interesting for the community.
Other Comments Or Suggestions: The Wayformer Ensemble metrics do not seem to fit to the Nayakanti et al. 2023 paper (which does not seem to be the Ensemble paper), the WOMD leaderboard of the challenge or the newer paper which should be the Wayformer Ensemble paper, "Scaling Motion Forecasting Models with Ensemble Distillation", Ettinger et al. (ICRA 2024). The results seem closest to the Nayakanti paper but this refers to older results from 2021. The authors should check the metrics (which are approximately correct not but 100%) and either correct or explain more specifically where they are coming from. There may be some confusion of what the Ensemble paper is.
Questions For Authors: The authors should remark on comments where something in the paper is lacking or missing.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely thank the reviewer for your detailed and thoughtful feedback. We appreciate the positive assessment of our work as a valuable contribution to the autonomous driving literature through our large-scale scaling experiments, with simple straightforward experimental design and good performance in WOMD and real driving.
We address your comments and questions below.
---
**Newer WOMD approaches**
We thank the reviewer for pointing this out. We will include more recent methods in the related works section and additional results including MTR++ in Table 4 in the final version.
While MTR++ introduces a set of novel techniques to improve upon MTR, our method outperforms MTR++ in terms of minADE, minFDE, and MR, as indicated by Table 4 of our paper and Table 1 in the MTR++ paper.
---
**Diminishing scaling returns**
We agree with the reviewer’s observations on diminishing returns, which have also been noted in the LLM literature, and we appreciate the positive feedback on this insight. These findings are an important part of the story we want to share with the community to encourage further research in this direction. In the final version, we will clarify this discussion and defer exploring additional scaling trends using more data samples as future work.
---
**Dataset details**
Our dataset is collected from multiple countries and cities across North America and Asia, primarily through urban driving, with data evenly distributed across day and night. To maintain anonymity for the double-blind review, we will provide more details on the countries and cities in the final version.
As noted on Page 4, Line 171, we process camera, LiDAR, and HD map data into vectorized representations. While the training data includes only vehicle driving, each scene is captured in dense urban environments containing numerous cyclists and pedestrians exhibiting diverse behaviors, such as jaywalking, blowthrough, and riding in the opposite lane, as shown in our qualitative examples.
We will include all requested dataset details in the final version and are happy to provide any additional information if the reviewer identifies any gaps.
---
**Figure 1 baseline**
The baseline is an 8M model using the same transformer architecture, trained on 2.2M data. We will clarify this in the final version.
---
**Closed-loop driving information**
We use DriveGPT to drive a car in real time, taking input features from a perception system that provides agent states and map information. While the full system incorporates additional components to handle long-tail events, we showcase challenging scenarios in the supplementary video where DriveGPT alone is responsible for driving, demonstrating its effectiveness.
We used the 8M model, trained on the full dataset, to drive the car, achieving a latency of under 50ms. While training the model requires 16 H100 GPUs with a batch size of 2048 (see Page 11, Line 559), real-time inference only requires a batch size of 1 and can run on a single onboard GPU.
We will include all requested details in the final version and are happy to provide any additional information if the reviewer identifies any gaps.
---
**Wayformer metrics**
The Wayformer results reported in Table 4 of our paper are sourced from Table 1 in “Real-Time Motion Prediction via Heterogeneous Polyline Transformer with Relative Pose Encoding” (Zhang et al., NeurIPS 2023). In that paper, the authors attributed the Wayformer results to [Nayakanti et al., 2023] and explicitly labeled them as ensemble in the table caption.
In [Nayakanti et al., 2023], the authors stated in Section 5.4: “We further apply ensembling, a standard practice for producing SOTA results for leaderboard submissions.” The numbers reported in Table 1 (last but second row, *LQ + Multi-Axis*) of [Nayakanti et al., 2023] match those in Table 1 of [Zhang et al., 2023], confirming consistency.
To prevent confusion with [Ettinger et al., 2024], we will rename "Wayformer Ensemble" to "Wayformer" and clarify the source of the baseline metrics in the final version. We will also include additional discussion on [Ettinger et al., 2024] in the related works section.
---
Thank you once again for your constructive comments. We hope that we have addressed your questions and that you will consider supporting the acceptance of our manuscript. | null | null | null | null | null | null | null | null |
Sparsing Law: Towards Large Language Models with Greater Activation Sparsity | Accept (poster) | Summary: This paper tackles activation sparsity in LLMs to boost efficiency. They introduce CETT-PPL-1%, a sparsity metric that keeps perplexity within 1% of dense models, cutting activations. They explore four factors (pre-training data, activation function, width-depth ratio, model scale) across 0.1B to 1.2B models, finding ReLU outperforms SiLU, more data sparsifies ReLU models, deeper models help sparsity up to a limit, and scale barely shifts sparsity caps.
## update after rebuttal
After careful consideration, I have decided to increase the score to "Accept." The lack of formal proof is not an issue at all. Also, I believe the paper has the potential to share valuable insights about increasing the activation sparsity. If the paper includes the references to the missing citations, the paper will give provide even more complete picture.
Claims And Evidence: The claims hold up. CETT-PPL-1% balances sparsity and performance—Figure 2 shows low PPL, and Table 1 keeps downstream scores near dense (avg. drop <0.5%). Factor findings are solid: ReLU beats SiLU (Figure 4), and the 2.4B model’s 93.52% sparsity (Section 6) follows their recipe. Thorough and extensive experiments were done to back the claims.
Methods And Evaluation Criteria: CETT-PPL-1% is clever—binary search tunes sparsity per layer works across ReLU and SiLU. They also conduct extensive experiments to find the activation sparsity scaling law. The extensive use of well-established benchmarks is also great.
Theoretical Claims: No formal proofs, just fits. ReLU’s logspace power-law (Eq. 4) and SiLU’s power-law (Eq. 5) match Figure 4, with coefficients in Appendix G. Scale-insensitivity leans on similar neuron patterns (Section 5.3), supported by Figures 9-10. Smaller models converging faster (Figure 8) tracks, but the grouping model (Eq. 6) is speculative—no math locks in why sparsity caps across scales.
Experimental Designs Or Analyses: Experiments are robust and extensive. A practical limitation would be that the experiment was limited to 2.4B model. Although not feasible, investigating the larger models could have provided more significant insights.
Supplementary Material: N/A
Relation To Broader Scientific Literature: They not only find the best activation sparsity technique, but also go beyond that by investigating the sparsity law. This sets them apart from the prior works that simply present a new sparsification technique. This paper has a potential to serve as a "sparsity scaling law" which can provide more insights into how to train a more sparse model. The paper's in-depth exploration of the four factors that affect activation sparisty is also helpful.
Essential References Not Discussed: "CATS: Contextually-Aware Thresholding for Sparsity in Large Language Models" and "Training-free activation sparsity in large language models" are simple post-training techniques for SiLU that find a layer-wise absolute threshold to accelerate LLM inference, that were concurrent works to "ReLU^2 wins." Citing this could provide a more complete picture of sparsifying SiLU.
Other Strengths And Weaknesses: While limited to smaller models (<=2.4B models), the paper provides insights into what affects the activation sparsity of language models. It is understandable that it is hard to study a model bigger than that. The experiments presented in the paper already suggests some meaningful insights on what affects activation sparsity.
Other Comments Or Suggestions: N/A
Questions For Authors: Q1. In Table 1, for a smaller ReLU model, why does CETT1% perform worse than CETT10%?
Q2. Can we extrapolate the scaling law for larger models?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your excellent review. These will encourage us to further improve the quality of our work and continuously forge ahead on the research path.
## Works in "Essential References Not Discussed"
Thank you for pointing out these two works! They are both related to our paper. We discuss these works here, and will cite them in our future versions.
CATS [1] seems to be a post-training sparsification method based on thresholds. However, after carefully reading the paper and codes, we find that CATS is exactly equivalent to the Top-$k$ setting in our experiments in Section 4.1 of our paper. Specifically, for each FFN layer, CATS will find a corresponding cutoff threshold that just controls the sparsity ratio at a desired level. The activations with smaller absolute values will be dropped. Therefore, this is the same as Top-$k$, which reserves the same ratio of activation values for each layer according to the absolute values.
TEAL [2] is a more interesting work. It proposes a completely different paradigm of activation sparsity. Concretely, TEAL focuses on the input sparsity, indicating that for each vector-matrix computation $\mathbf{x}\mathbf{W}^T$, the values at some positions of $\mathbf{x}$ are small, and computation corresponding to these positions can be skipped for acceleration. By contrast, our work focuses on output sparsity, indicating the highly sparse patterns in the output $\sigma(\mathbf{x}\mathbf{W}_{gate}^T)$ of FFN activation functions. Since these two paradigms have completely different definitions of activation sparsity, the sparsity ratios cannot be trivially compared, and the properties (e.g., scaling laws) of them are also different. We are willing to open a new work to study such input sparsity in the future.
## Lack of Formal Proofs in "Theoretical Claims"
Thank you for pointing out the lack of formal math proofs in our work. We believe that more strict theoretical works are valuable and indispensable in the future. However, at present, LLMs are black-box systems, which are extremely difficult to interpret theoretically. Instead, mainstream works find empirical laws using statistical methods to make the LLM behavior more predictable. Strict math models are hard to build, as the huge parameter scales make LLMs a highly complex system. The study of human brains also encounters similar challenges, and the statistical analysis of signals like brain waves becomes the mainstream paradigm. Still, we admit the value of more rigorous and formal math modeling and will make our analyses more convincing.
## Question 1
Considering the general ability, the PPL used to measure sparsity is evaluated on a general validation set with the same distribution as the training set, covering a wide variety of corpus. However, a lower average PPL on the general data cannot necessarily ensure better performance on a specific category of downstream tasks. In Table 1, the performance of reading comprehension consistently drops with an increasing PPL, but the scores of commonsense reasoning fluctuate. Such a phenomenon will be more significant for those tasks accounting for a smaller part of the training data.
## Question 2
Some coefficients in our activation-data power-laws can potentially be extrapolated to larger models.
First, the limit activation ratio $A_0$ is clearly weakly correlated to the parameter scale. This is also an important finding already stated in this article.
Besides, by Table 2, for ReLU-activated models, the coefficient $\alpha$ monotonically increases, while $c$ monotonically decreases with the model scale. Coefficient $b$ seems to have little value fluctuation when the model scale is larger than 0.4B. These indicate that there probably exist quantitative relationships between these coefficients and the model scale, or in other words, we may incorporate the model scale into our scaling law. However, finding a well-fit law including the model scale is too expensive, as dozens of scales of models should be trained for data preparation. Even the most famous work on scaling laws by OpenAI [3] did not cover model scales larger than 2B.
## References
[1] Lee, Donghyun, et al. "CATS: Contextually-aware thresholding for sparsity in large language models." *arXiv preprint arXiv:2404.08763* (2024).
[2] Liu, James, et al. "Training-free activation sparsity in large language models." *arXiv preprint arXiv:2408.14690* (2024).
[3] Kaplan, Jared, et al. "Scaling laws for neural language models." *arXiv preprint arXiv:2001.08361* (2020). | Summary: This paper investigates activation sparsity in LLMs through extensive experiments. The main findings include:
1) A quantitative analysis of sparsity patterns across model scales and width-depth ratios;
2) The relationship between activation sparsity ratio and data scale;
3) Achievement of a 93.52% sparsity ratio and 4.1× speedup compared to the dense model on a 2.4B parameter model using CETT-PPL-1%.
## update after rebuttal
Thanks for the authors' responses, which address most of my concerns. I have decided to increase the score.
Claims And Evidence: Yes, the sparsity analysis is backed by comprehensive measurements across different model scales.
Methods And Evaluation Criteria: The evaluation methods are appropriate. However, the evaluation framework for activation sparsity is directly adopted from previous work (CETT), with this study merely finding optimal hyperparameters under a specific experimental setting (PPL increase tolerance of p%). Besides, the reported 4.1× speedup on a 2.4B parameter model lacks convincing evidence for real-world application scenarios.
Theoretical Claims: The paper does not present any theoretical proofs for its claims.
Experimental Designs Or Analyses: The experimental designs are valid.
Supplementary Material: Reviewed implementation details and additional experimental results in supplementary materials.
Relation To Broader Scientific Literature: The work appears to be an extension of CETT's findings on ReLU sparsity. While it provides more comprehensive analysis, it doesn't present fundamentally new insights or directions.
Essential References Not Discussed: The paper has appropriately cited and discussed the key related works. No significant omissions were found in the literature review.
Other Strengths And Weaknesses: The analysis is comprehensive, with experimental investigations across different model scales and detailed examinations of sparsity patterns. The paper is well-structured.
However, the work primarily extends existing work (CETT) without introducing fundamentally new concepts and focuses more on analysis rather than proposing new solutions.
Other Comments Or Suggestions: While the authors clearly differentiate their work from MoE and parameter pruning, two potential improvements were overlooked: (1) exploring combinations with other optimization techniques could yield more substantial improvements beyond the 4.1× speedup; (2) demonstrating practical applications would better justify the research value.
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your excellent review. These will encourage us to further improve the quality of our work and continuously forge ahead on the research path.
## Practical Acceleration using Activation Sparsity
In Section 6, we present an acceleration experiment based on our 2.4B sparsely-activated model, achieving a 4.1$\times$ speedup ratio. This is conducted on the machine with 1 NVIDIA A800 GPU and PowerInfer, a SOTA sparsity-based framework. As pointed out by the reviewer, there may exist gap between this setting and real-world application scenarios. Therefore, we conduct new acceleration experiments under the following setting: (1) We use the device **"NVIDIA Jetson Orin NX", a real-world representative end-side device tailored for AI**. (2) We combine activation sparsity with **Q4 quantization**, a mainstream acceleration technique.
The decoding speeds (token/sec) of the 2.4B model on NVIDIA Jetson Orin NX are shown in the following table:
| Dense (llama.cpp) | Sparse (PowerInfer) | Sparse (PowerInfer+Q4) |
| :---------------: | :-----------------: | :--------------------: |
|5.42|8.76|10.97|
Using activation sparsity, we achieve a considerable speedup compared to the dense setting. Moreover, activation sparsity can also be combined with quantization and achieve an even higher decoding speedup.
Finally, we admit that the combination of activation sparsity and some other acceleration methods is non-trivial. For example, we are already working on its combination with speculative decoding. In this case, we use a new auxiliary loss to increase the similarity between activation patterns of neighbor tokens. With such modification, we are able to effectively utilize activation sparsity to further promote the efficacy of speculative decoding.
## Contributions of This Work
**Our work is not a mere extension of previous work CETT.** Instead, we expect this work to be the foundation of future works involving the **measurement, analysis, and training of sparsely-activated LLMs**. Specifically, we give answers to three important questions:
- How can activation sparsity be measured more accurately?
We present a new perspective on activation sparsity: **sparsity is the function of performance and must be measured under a specific tolerance of performance drop (i.e., PPL increase)**. Most existing works focus on ReLU-based activation sparsity, considering sparsity a fixed value with no connection to performance. After that, "ReLU$^2$ Wins" proposes CETT [1], enabling us to evaluate the sparsity of non-ReLU LLMs, as sparsity is considered a function of CETT.
Admittedly, in terms of methodology, our CETT-PPL-1% mainly introduces a hyper-parameter search process, finding an appropriate CETT value under a PPL increase ratio. This conversion is simple but important, as sparsity is finally linked to performance, and we are able to inspect the sparsity of LLMs under a specific expectation of performance. After all, it is more intuitive and reasonable to measure sparsity from the lens of performance rather than the ambiguous CETT. Otherwise, it will be complicated to compare the sparsity of models with different architectures (e.g., measuring the sparsity at multiple CETT points and comparing the Pareto curves).
- How is activation sparsity affected by the model architecture and training process?
We present a systematic quantitative analysis of the influential factors of activation sparsity, including the activation function, amount of training data, parameter scale, and width-depth ratio. Analytical scaling laws are also found between sparsity and the amount of training data under ReLU and SiLU. These findings are the basis of the third question.
- How can we build a more sparsely-activated and efficient LLM?
As the most important long-term contribution of this work, based on the above findings, **we propose the better approach to obtaining more sparsely-activated LLM**: Use ReLU as the activation function with a larger amount of pre-training data, and a small width-depth ratio within the interval ensuring the training stability. We also pre-train a 2.4B model from scratch, with an extremely low activation ratio of 6.48%, to re-validate our findings. Our work can provide instructional values for designing and pre-training an LLM with greater activation sparsity, which helps produce more efficient LLMs.
## References
[1] Zhang, Zhengyan, et al. "ReLU$^ 2$ Wins: Discovering Efficient Activation Functions for Sparse LLMs." *arXiv preprint arXiv:2402.03804* (2024). | Summary: This paper addresses three main directions related to activation sparsity. First, they introduce a new metric which they show to be better than existing activation sparsity metrics. Then, they explore the relationship between various details of the training process with the ability for a model to achieve high activation sparsity. Finally, they demonstrate that through a combination of various features discovered in the second direction, they are able to train a highly sparse LLM with an activation ratio of 6.48% with minimal performance degradation (ie at most 1% increase in perplexity).
## Update after Rebuttal
No additional comments, the authors answered my questions and I maintain my score.
Claims And Evidence: Yes, for the most part I think the claims are supported by evidence. One additional experiment I would like to see is a side-by-side comparison of LLM training as proposed in section 6 with a baseline and/or ablations of each of the components. I understand this is likely infeasible in the rebuttal period but it would be nice to see a direct comparison of even a much smaller LLM trained from scratch if possible. To be clear, if this is not computationally feasible within the time frame, it will not affect my final score.
Methods And Evaluation Criteria: Yes, methods and evaluation criteria both make sense.
Theoretical Claims: There are no theoretical claims that need to be checked.
Experimental Designs Or Analyses: Yes, the experimental design and analysis seem sound. The paper clearly goes through each component, providing evidence for each claimed relationship to activation sparsity.
Supplementary Material: I did not need to reference the supplementary material to understand the paper but I skimmed it briefly and it adds some nice additional details.
Relation To Broader Scientific Literature: The most relevant tie to previous literature is building upon the CETT metric to develop their proposed metric, CETT-PPL-1%. Otherwise, it seems to contribute a nice set of findings to both the activation sparsity and scaling law literature.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: I think this paper is well structured and written. It has novelty in the proposal of a new metric, it backs up this metric with experimental evidence of its superiority, and provides general principles/guidelines with experimental evidence.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your excellent review. These will encourage us to further improve the quality of our work and continuously forge ahead on the research path.
## Ablation Studies in "Claims And Evidence"
Thank you for reminding us of the ablation studies on the 2.4B model. As it is really expensive to pre-train a new 2.4B model from scratch, we'd like to re-state the results on smaller models for each ablation factor. Most of these are already presented in the current manuscript.
As mentioned in Section 6, we consider 3 factors: (1) ReLU as the activation function; (2) a larger amount of training data; (3) a small width-depth ratio within the interval ensuring the training stability.
### Activation Function
For each size among "0.1B, 0.2B, 0.4B, 0.8B, 1.2B", as shown in Figure 7, **replacing ReLU with SiLU can cause a considerable increase in the activation ratio by more than 30%**, indicating worse sparsity. Note that these two activation functions do not have significant performance differences by task performance (Table 1) and training loss (Figure 14).
Specifically, we present the limit activation ratio (%) of the 0.1B/0.2B models with different activation functions in the following table. Clearly, **ReLU has significantly higher sparsity than commonly used SiLU and GELU**.
| | ReLU | SiLU | GELU |
| :--: | :--: | :--: | :--: |
| 0.1B | 6.14 | 40.9 | 33.3 |
| 0.2B | 6.74 | 39.0 | 34.2 |
### Amount of Training Data
For each size among "0.1B, 0.2B, 0.4B, 0.8B, 1.2B", as shown in Figure 4, the ReLU-activated models always display lower activation ratios (i.e., higher sparsity ratios) with the increase in the amount of training data. This fact is re-validated in the 2.4B model. Figure 11 indicates that 2.4B has a similar negative relationship between the activation ratio and the amount of training data. Therefore, **a decrease in the amount of training data can cause a sparsity drop for ReLU-activated models**.
### Width-Depth Ratio
We conduct a systematic study on the relationship between sparsity and the width-depth ratio in Section 5.2. As shown in Figure 5 and Figure 6, for the 0.1B ReLU-activated model, the limit of activation ratios linearly increases with the width-depth ratio before a bottleneck point 114, and the lowest training loss with training stability can be achieved within the interval [74, 282]. The 2.4B model as well as other settings from 0.2B to 1.2B all adopt a width-depth ratio close to the smallest point of the training stability interval. In 0.1B experiments, this setting is demonstrated to have the lowest activation ratio under the premise of training stability. **A smaller width-depth ratio than this can cause training instability and worse performance, and a larger one brings about a sparsity drop.** | null | null | null | null | null | null | null | null |
Provable Efficiency of Guidance in Diffusion Models for General Data Distribution | Accept (poster) | Summary: This paper presents a theoretical analysis of classifier-free guidance (CFG) in diffusion models, demonstrating that guidance enhances sample quality by reducing the expected ratio of poor samples, as measured by classifier probability. The authors establish a connection between their proposed metric and the Inception Score, a widely used evaluation metric for diffusion model sample quality, thereby justifying the choice of their metric. To validate their theoretical findings, the authors provide a one-dimensional experiment involving Gaussian Mixtures, which serves as a proof-of-concept for their approach.
Claims And Evidence: The main result, Theorem 3.1, appears to be theoretically sound and relevant to the current literature on classifier-free guidance (CFG). However, I am concerned that the paper lacks sufficient empirical evidence to support this theoretical contribution. The experimental section is unfortunately very weak, which undermines the overall impact of the paper. To strengthen the manuscript, I would recommend that the authors invest significant effort into improving the experimental evaluation, including more comprehensive and rigorous experiments that demonstrate the practical effectiveness of their approach. Furthermore, giving more detailed insight and explanation regarding the main theorem and its contribution would benefit for the future readers. In its current form, I do not believe that the paper meets the standards expected for an ICML conference paper.
Methods And Evaluation Criteria: Unfortunately, the paper falls short in its experimental evaluation. The authors only present a single experiment on a one-dimensional Gaussian Mixture, which is insufficient to demonstrate the effectiveness of their approach. To strengthen the paper, I would recommend that the authors conduct additional experiments on higher-dimensional models, including Gaussian Mixtures, as well as real-world datasets. This would provide a more comprehensive understanding of the proposed method's performance and limitations.
Furthermore, I have concerns regarding the example presented on page 8. The authors claim that P(p_{c|X_0}(1|Y_0^w) \geq p_{c|X_0}(1|Y_0^0)) is less than one, but the curve suggests that this may not be the case for sufficiently large values of w. Moreover, this specific scenario has been previously analyzed in "What does guidance do? A fine-grained analysis in a simple setting" by Chidambaram et al., who demonstrated that classifier-free guidance (CFG) in one dimension can lead to flawed results, including mean overshoot and variance shrinkage. In light of these findings, it is essential that the authors perform experiments in larger dimensions and on real-world datasets to validate their claims and demonstrate the robustness of their approach.
Theoretical Claims: I did not find an error in the calculations in the paper.
Experimental Designs Or Analyses: There is only one experiment in one dimension. As mentioned above, even this experiment and its results do not seem completely valid.
Supplementary Material: The supplementary material consists of only one page and I have read it.
Relation To Broader Scientific Literature: There is currently an increasing amount of theoretical works that are attempting to explain CFG, so this paper is timely and relevant.
Essential References Not Discussed: It is disappointing that the authors have not cited any related work, especially given the substantial body of research currently focused on explaining classifier-free guidance (CFG) from a theoretical perspective. For instance, relevant studies can be found in the following papers: https://arxiv.org/abs/2409.13074, https://arxiv.org/abs/2403.01639, and https://arxiv.org/abs/2408.09000. Including references to these works would provide valuable context and strengthen the paper's contribution to the field.
Other Strengths And Weaknesses: I would also strongly advise the authors to move all the proofs to the appendix and to only highlight the main results in the main paper, as well as add related work and stronger experimental results.
Other Comments Or Suggestions: The authors justify their chosen metric by demonstrating its relationship to the Inception Score. However, it is important to note that the Inception Score is considered outdated and is no longer widely used in recent work on diffusion models. For instance, a well-known study in the field highlights the shortcomings of this metric https://arxiv.org/pdf/1801.01973. I strongly recommend that the authors address this issue by discussing the relevance of their metric in light of these criticisms and by relating the findings of their paper to the proposed metric. This would help clarify the metric's applicability and strengthen the paper's contribution.
There is a typo on end of page 2, where you have double brackets )) and should have just one: ∇ log pc | Xn (c | x)).
Your title is "Title Suppressed Due to Excessive Size" so please make sure to amend this accordingly.
Page 2 also mentions multiple times that Z_n represents i.i.d. Gaussian noise, this could be avoided for conciseness and clarity.
Questions For Authors: No questions.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: Thanks for your valuable questions. Below we provide a detailed point-by-point response.
**Experiments on real dataset.** We have added experiments on the ImageNet dataset to validate our theory. Please refer to our response to Reviewer EKNn of **Experiments on real dataset**.
**Further explanations of the main theorem.**
We agree that a more detailed explanation of Theorem 3.1 would enhance clarity. In the revised version, we will add the explanation of main analysis idea (see ''Explanation of main analysis idea'' in our response to Reviewer 5U8H), detailed comparison with prior theory (see ''Comparison with prior works'' in this response), explanation of IS (see ''Issue of Inception Score'' in this reponse), and experiments on Imagenet dataset (see ''Experiments on real dataset'' in our response to Reviewer EKNn) to address this comment.
**Clarification of the toy example.**
Originally, we state that *''$P(p_{1|X_0}(1|Y_0^w)\ge p_{1|X_0}(1 | Y_0^0))$ is less than $1$, which indicates the guidance may not achieve uniform improvement in classifier probabilities''* for the toy example. To make it more accurate, we will revise it to *''$P(p_{1 | X_0}(1| Y_0^w)\ge p_{1| X_0}(1| Y_0^0)) < 1$ for any $w < 10$, which indicates ...''*, since we have numerically confirmed that this holds true for all $w < 10$, which covers the practical range of $w$ in typical applications.
**Relation to prior works on toy examples.** We agree with the existence of prior analyses of classifier guidance in GMMs. However, our work focuses on different aspects compared to these studies.
We will include a detailed comparison in the revised version, as detailed in next bullet.
**Comparison with prior works.** Actually, we have cited and briefly compared with these existing works, which mainly focus on specific classes of distributions like GMMs. In contrast, our main contribution lies in providing a more general theoretical analysis. Nonetheless, we agree that a comparison between our theory--- when applied to specific distributions--- and prior works would further clarify our contributions. We will include a new section in the revised manuscript for comparison:
''Existing works focus mainly on specific classes of distributions like GMMs, while our work provides a more general theoretical analysis. Below, we compare our findings with prior works when restricted to specific distributions.
In [1], the authors demonstrate that $p_{c | X_0}(c | Y_1^w)\ge p_{c | X_0}(c | Y_1^0)$ holds under specific conditions, while we show that this inequality does not always hold. In addition, [2] argues that guidance can degrade the performance of diffusion models, as it may introduce mean overshoot and variance shrinkage. In contrast, our result shows that guidance can improve sample quality by generating more samples of high quality. Furthermore, [3] shows that classifier guidance can not generate samples from $p(x | c)^{\gamma}p(x)^{1-\gamma}$ for GMMs and establishes its connection to an alternative approach, i.e., the single-step predictor-corrector method, whose effectiveness in this specific setting remains unclear. In contrast, we directly analyze and demonstrate the effectiveness of CFG.''
**Issue of Inception Score (IS).**
We offer two clarifications:
1. The reviewer is absolutely correct that IS is not a perfect metric and has known limitations in evaluating sample quality.
2. We disagree that *''IS is outdated''* and argue that IS is still one of the most widely used and informative metrics for assessing sample quality. The precise evaluation of sample quality remains an open problem. Despite the concerns raised in [4], IS continues to be employed as a key metric in recent works on classifier guidance [5] and classifier-free guidance [6] for diffusion models, due to the absence of an alternative metric that is demonstrably superior to IS. Our choice to consider IS aligns with the original studies that introduced diffusion guidance. In addition, most issues outlined in [4] come from the inaccuracy in the empirical estimation of IS, which doesn't apply for the theoretical consideration, as our results are derived using the true conditional probability.
We will clarify the reasonability for using IS in the revised manuscript:
''Although some practical limitations of IS have been identified [4], it remains a commonly used metric for evaluating sample quality in the study of diffusion guidance [5,6]. Moreover, in our theoretical analysis, we use the true conditional probability, which addresses the estimation issues discussed in [4].''
**Typos.** We have fixed them in the revised version.
[1] Theoretical Insights for Diffusion Guidance: A Case Study for Gaussian Mixture Models
[2] What does guidance do? A fine-grained analysis in a simple setting
[3] Classifier-Free Guidance is a Predictor-Corrector
[4] A Note on the Inception Score
[5] Diffusion Models Beat GANs on Image Synthesis
[6] Classifier-free diffusion guidance
---
Rebuttal Comment 1.1:
Comment: Thank you for the response. Regarding IS, most of the papers which you cite are in my opinion outdated. The recent works, particularly those on state-of-the-art class conditional models (or even text-to-image) diffusion models consider Inception Score to be an outdated metric. I strongly advise the authors to consider other metrics.
Although I believe that there is a contribution to the literature by your developed, I believe that the paper still falls short of the bar of acceptance, particularly due to its weak empirical evaluations.
---
Reply to Comment 1.1.1:
Comment: Thanks for your response. We greatly appreciate the time and effort you have dedicated to reviewing our paper.
**Further response on IS.**
In our previous response, we stated that [5] and [6] introduced classifier(-free) guidance to enhance sample quality by balancing fidelity and diversity, where IS is employed as a key evaluation metric. This motivates our study on the improvement of classifer probability, i.e., $p(c|x)$. In addition, [1], published in ICML last year, also investigated improvements in classifier probability $p(c|z)$ (see Section 3). Moreover, most of the issues with IS discussed in [4] stem from the estimation of $p(c | x)$, which does not applicable for theoretical analysis. Hence, we believe that analyzing the effectiveness of guidance through improvements in classifier probability remains a valuable research direction in this field.
You said that IS is considered outdated for class-conditional models, including text-to-image models, but did not mention its status in recent works on diffusion guidance. It would be much appreciated if you can provide any recent works that study the effectiveness of diffusion guidance and provide evidence that classifier probability is an inappropriate metric in this context.
**Further response on experiments.**
We would like to emphasize that this work is theoretical, providing the first theoretical guarantee on the effectiveness of diffusion guidance for general data distributions. While our focus is on theoretical analysis, we have supplemented our findings with empirical validation using both a toy example (GMM) and a real-world dataset (ImageNet). We believe these experiments sufficiently support our theoretical results. For comparison, prior theoretical work on diffusion guidance [1], which was published at ICML last year, conducted experiments only on GMMs. Given this precedent, we believe our empirical evaluations are appropriate for a theoretical study. | Summary: This paper gives a novel theoretical analysis of classifier guidance. Whereas prior work focused on special cases, e.g. mixtures of Gaussians and compactly supported distributions, this paper establishes a guarantee under minimal distributional assumptions. Specifically, they consider the functional given by the expected *inverse* classifier probability over generated samples, which is correlated with sample quality, and show that this quantity decreases as the guidance parameter increases. The analysis is short but clever: they utilize th
Claims And Evidence: Yes, please see "Theoretical Claims" for details
Methods And Evaluation Criteria: N/A as this is a theory paper
Theoretical Claims: I checked the correctness of the proof of Theorem 3.1, the main calculation for which appears in Section 4, and believe it to be sound. Please see "Strengths and Weaknesses" for further thoughts on the theory.
Experimental Designs Or Analyses: The experiment was a small-scale evaluation for Gaussian mixtures, and the results appear to be valid and consistent with the theoretical findings.
Supplementary Material: Yes, the supplement was just routine calculations with Girsanov's theorem and with score functions for Gaussian mixtures.
Relation To Broader Scientific Literature: This paper fits into the broader literature on establishing rigorous guarantees for diffusion models.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths:
- This paper's main selling point is that it gives a guarantee for guidance that works for all probability distributions. This is quite exciting, as all prior work focused on specific classes of distributions like Gaussian mixtures, and prior to reading this paper I would not have expected one can prove any interesting, general-purpose result about classifier guidance.
- The key idea is quite clean: (1) the functional they consider is a martingale along the unguided reverse process, so its infinitesimal expected change (which is zero) can be approximated to first order, using Ito's lemma, by an expression depending only on its derivatives in time/space. (2) Likewise, the infinitesimal expected change for the guided reverse process can be approximated to first order using a very similar expression, with some extra terms arising from the guidance term. These extra terms are precisely what give rise to the decrease in expected inverse classifier probability under guidance.
Weaknesses:
- The writing does not do a good job of communicating the main idea behind the calculations in an easy-to-understand manner. I am happy to raise my score if the authors can improve the clarity of the writing
- Unless I'm misunderstanding, the analysis is specific to DDPMs and does not say anything about DDIMs.
- While the authors show the discrete and continuous-time samplers are close using off-the-shelf methods, it's not clear how this closeness can be combined with the main result on expected inverse classifier probability to say something about how that functional behaves under guidance for discrete-time samplers.
Other Comments Or Suggestions: Please see "Weaknesses" and "Questions for Authors"
Questions For Authors: - Could you comment on how to combine Theorem 3.1 with Theorem 3.6? It's not clear to me that the KL bound should imply anything about the expected inverse classifier probability. I guess if the inverse classifier probability is bounded, then you can use Pinsker's, but such boundedness doesn't seem to be a reasonable assumption.
- Have you tried assessing whether expected inverse classifier probability is actually meaningful in real data? I would imagine it's too large in general to be a useful measure of distributional sample quality
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank the reviewer for the constructive feedback! Below, we provide a detailed point-by-point response.
**Explanation of main analysis idea.** In the revised version, we will add the following explanations to better communicate the high-level ideas behind the analysis:
''**A glimpse of the main analysis idea.** First, this result comes from the key observation that the function of reverse process, $p_{c|X_{t}}(c|X_t)^{\rm -1}$, forms a martingale, as stated in Lemma 3.2, which is established through a careful decomposition of $p_{c|X_{t}}$ and $p_{X_{\tau}|X_{t}}$. Next, the guidance term $s_t(x|c) - s_t(x)$ in classifier-free guidance (CFG) aligns with the direction of $-\nabla p_{c| X_t}(c| x)^{-1} = p_{c| X_t}(c| x)^{-1}[s_t(x|c) - s_t(x)]$, which makes us expect that adding the guidance at time $t$ can decrease $\mathbb{E}\_{x_{\tau} \sim X_{\tau}}\big[p_{c| X_{\tau}}(c| x_{\tau})^{-1} | X_t = x\big]$ for all $\tau \le t$. Finally, to achieve the desired result, particular care must be taken in handling first- and second-order differential terms with respect to $t$ for the process $p_{c| X_{1-t}}(c| Y_t^w)^{-1}$ due to its randomness nature, which is completed in Section 4.2 based on the technique of Ito's formula.''
**Extension to DDIM.** As pointed out by the reviewer, our analysis is specific to DDPMs. In particular, our analysis relies on the martingale property stated in Lemma 3.2, which relies heavily on the property of $p_{X_{\tau}|X_{t}}$ in DDPMs and can not be applied for DDIMs. Extending our framework to DDIMs remains an open question due to the absence of this key property. We will add a remark in Section 3.1 of the revised version to explicitly state this limitation.
**Influence of discretization.** We fully agree that our continuous-time analysis for CFG can not be immediately extended to the discrete-time setting with only small KL divergence error. As the reviewer suggests, if $p(c | x)^{-1}$ is uniformly bounded, one could establish the desired result. However, such an assumption is too strong. Instead, we adopt a weaker condition: we assume that $\mathbb{E}[(p(c | Y_1^w)^{-1}-1)1(p(c | Y_1^w)^{-1} > \tau)]$ is small for some threshold $\tau > 0$. We have also verified this assumption numerically on the Imagenet dataset. We will include the following new result in the revised version:
''The sampling process (5) with the learning rate schedule (19) satisfies
\begin{align*}
\mathbb{E}[p(c | Y_1^w)^{-1}] \le \mathbb{E}[p(c | Y_{\overline\alpha_1}^{w, \mathsf{cont}})^{-1}] + \mathbb{E}[(p(c | Y_{1}^{w})^{-1}-1)1(p(c | Y_{1}^{w})^{-1} > \tau)],
\end{align*}
where $\tau$ is defined as the largest value satisfying
\begin{align*}
\mathsf{TV}(Y_{\overline\alpha_1}^{w, \mathsf{cont}}, Y_1^w) \le \mathbb{P}(p(c | Y_{1}^{w})^{-1} > \tau).
\end{align*}
This further implies the following relative influence from discretization, the ratio between the improvements of $Y_1^w$ and $Y_{\overline\alpha_1}^{w, \mathsf{cont}}$ over $X_{\overline\alpha_1} = Y_{\overline\alpha_1}^{0, \mathsf{cont}}$, obeys
\begin{align*}
\frac{\mathbb{E}[p(c | Y_{\overline\alpha_1}^{0, \mathsf{cont}})^{-1}] - \mathbb{E}[p(c | Y_1^w)^{-1}]}{\mathbb{E}[p(c | Y_{\overline\alpha_1}^{0, \mathsf{cont}})^{-1}] - \mathbb{E}[p(c | Y_{\overline\alpha_1}^{w, \mathsf{cont}})^{-1}]}
\ge 1 - \frac{\mathbb{E}[(p(c | Y_{1}^{w})^{-1}-1)1(p(c | Y_1^w)^{-1} > \tau)]}{\mathbb{E}[p(c | Y_{\overline\alpha_1}^{0, \mathsf{cont}})^{-1}] - \mathbb{E}[p(c | Y_{\overline\alpha_1}^{w, \mathsf{cont}})^{-1}]}.
\end{align*}
For different values of $\mathsf{TV}(Y_{\overline\alpha_1}^{w, \mathsf{cont}}, Y_1^w)$, we empirically validate the aforementioned assumption on the ImageNet dataset. Here we use $\mathbb{E}[p(c | Y_{1}^{0})^{-1}]-\mathbb{E}[p(c | Y_{1}^{w})^{-1}]$ as an estimate of $\mathbb{E}[p(c | Y_{\overline\alpha_1}^{0, \mathsf{cont}})^{-1}] - \mathbb{E}[p(c | Y_{\overline\alpha_1}^{w, \mathsf{cont}})^{-1}]$. The relative error $\frac{\mathbb{E}[(p(c | Y_{1}^{w})^{-1}-1)1(p(c | Y_1^w)^{-1} > \tau)]}{\mathbb{E}[p(c | Y_{1}^{0})^{-1}]-\mathbb{E}[p(c | Y_{1}^{w})^{-1}]}$ is presented in the following table for various values of the TV distance and $w$. The results indicate that the relative error remains small, particularly for practical choices of $w \ge 1$.
\begin{align*}
\begin{array}
\\hline
\\hline
\mathsf{TV} & w=0.2 & 0.4 & 0.6 & 0.8 & 1 & 2 & 3 & 4\\\\
\\hline
0.30 & 0.447 & 0.196 & 0.115 & 0.085 & 0.029 & 0.006 & 0.006 & 0.002 \\\\
0.10 & 0.440 & 0.194 & 0.114 & 0.085 & 0.029 & 0.006 & 0.005 & 0.002 \\\\
\\hline
\end{array}
\end{align*}
''
**Assessment on real dataset.** We have added experiments on the ImageNet dataset to validate our theory. Please refer to our response to Reviewer EKNn of **Experiments on real dataset**.
---
Rebuttal Comment 1.1:
Comment: Thanks for the new experiments and the thoughtful rebuttal. I have raised my score to a 4.
---
Reply to Comment 1.1.1:
Comment: Thank you for your acknowledgment and positive evaluation of our work! Your review comments are very helpful in improving the quality of our paper, and we will incorporate your suggestions into the revised manuscript. | Summary: In this paper, the authors analyze the effect of diffusion guidance under general data distributions. Their study reveals that guidance does not necessarily improve sample quality in all cases, but it enhances overall sample quality. Specifically, they prove that under the influence of guidance, the proportion of low-quality samples (measured by classifier probabilities) decreases. A toy experiment on the Gaussian Mixture Model provides empirical support for their theoretical analysis.
Claims And Evidence: Each claim in this paper is supported by strong theoretical justification.
Methods And Evaluation Criteria: This paper provides a sound theoretical analysis of the effect of guidance across general data distributions, offering valuable insights and contributions to the research community. Its findings are likely to inspire further advancements in the field.
Theoretical Claims: The theoretical analysis in this paper is sound, with detailed and correct proof processes or relevant literature support.
Experimental Designs Or Analyses: The experimental results are reliable—I did not find any obvious issues. However, although this paper primarily focuses on theoretical analysis and proofs, its experimental evaluation is relatively limited. The paper provides only a single case study on a Gaussian Mixture Model, which may not sufficiently demonstrate the practical applicability of the proposed method. Including experiments on more general data distributions would help readers better understand the method and provide stronger inspiration for the research community.
Supplementary Material: The supplementary materials include detailed proofs of the equations presented in the paper and implementation details of the related experiments, providing comprehensive explanations for aspects that could not be fully elaborated in the main text.
Relation To Broader Scientific Literature: This paper analyzes the effect of guidance on the sampling process in terms of the reciprocal of classifier probabilities, which, to some extent, is conceptually similar to the Inception Score. Moreover, compared to other works, such as Autoguidance [1], which only provide a qualitative analysis of the classifier-free guidance sampling process, this paper offers a detailed and rigorous theoretical analysis, making a more substantial contribution to the understanding of guidance in diffusion models.
[1]: Guiding a Diffusion Model with a Bad Version of Itself
Essential References Not Discussed: The citations and comparisons with related works are comprehensive and well-covered, ensuring a thorough contextualization of the proposed approach within the existing literature.
Other Strengths And Weaknesses: **Strengths**
1. The paper is written in a clear and coherent manner.
2. The paper provides a sound and comprehensive analysis of the effect of guidance mechanisms on general data distributions. The analysis is thorough and well-structured, offering valuable insights that could significantly inspire further research in the community.
3. The Toy Example on the Gaussian Mixture Model is a notable highlight of the paper, providing practical support for the theoretical analysis.
**Weaknesses**
1. Although the theoretical analysis in this paper is detailed and comprehensive, the Toy Experiments on the Gaussian Mixture Model alone feel somewhat limited. Conducting experimental analyses on more general data distributions and larger-scale models would provide stronger empirical validation, making the findings more impactful and accessible for the research community and readers.
Other Comments Or Suggestions: 1. Reorganizing the structure of the paper could enhance readability and comprehension. For example, presenting the Toy Experiments as a separate section rather than embedding them within the theoretical analysis would make it easier for readers to follow the logical flow of the paper.
Questions For Authors: 1. How can the theoretical analysis and insights from this paper be used to enhance the capability of the guidance mechanism in practical applications?
2. In my view, $\omega$ is a crucial hyperparameter in classifier-free guidance. When $\omega$ is too small, the generated samples do not align well with the conditions, while an excessively large $\omega$ affects the realism of the generated samples. The experiments conducted on GMM in this paper cover a wide range of $\omega$, and the evaluation metrics improve as $\omega$ increases, which seems inconsistent with observations in practical applications. Could you explain this discrepancy?
3. Could you provide experimental observations on more general benchmarks, such as MNIST or CIFAR-10?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks a lot for the reviewer's helpful comments and valuable feedback.
Below, we provide a point-by-point response, which has also been incorporated into the revised version of our manuscript.
**Experiments on real dataset.**
Notice that classifier-free guidance (CFG) was originally validated on the ImageNet dataset [1], where Inception Score is typically computed using the Inception v3 classifier [2]. To further support the practical applicability of our method, we have included an additional numerical experiment using a pre-trained diffusion model [3] on the ImageNet dataset, which we believe provides stronger empirical validation than other datasets.
The results demonstrate that guidance improves sample quality by decreasing the averaged reciprocal of the classifier probability rather than achieving uniform improvement across all samples, thereby validating our theory.
We adopt the guidance scale range in [1] from $0$ to $4$; specifically, in our experiments, we use $w = \{0.2, 0.4, 0.6, 0.8, 1, 2, 3, 4\}$.
The numerical results are as follows:
\begin{align*}
\begin{array}{c|cccccccccccc}
\\hline
\\hline
w & 0.2 & 0.4 & 0.6 & 0.8 & 1 & 2 & 3 & 4 \\\\
\\hline
{P(p_{c|X_0}(c|Y_1^w) \geq p_{c|X_0}(c|Y_1^0))} & 0.70 & 0.75 & 0.78 & 0.80 & 0.82 & 0.85 & 0.85 & 0.86 \\\\
-\mathbb{E}[p_{c|X_0}(c|Y_1^w)^{-1}] &-140 & -74 & -47 & -36 & -14 & -3.6 & -3.4 & -2.0 \\\\
\\hline
\end{array}
\end{align*}
**Paper structure.**
We agree that presenting the numerical experiments as a separate section would enhance readability.
we will restructure the manuscript by placing the toy experiment and the newly added results on the ImageNet dataset in a separate section following the main results.
**Practical implementation.**
One potential application of our theoretical analysis comes from its implication that guidance may reduce sample quality for a small subset of samples.
This observation could motivate further research into adaptive guidance mechanisms that ensure a more uniform improvement in sample quality.
We will include a remark following Theorem 3.1 to discuss the potential implementation of our theory:
''Theorem 3.1 states that guidance improves the averaged reciprocal of the classifier probability rather than the classifier probability of each individual sample. This suggests that while guidance improves overall sample quality, it may lead to a decline in quality for a small subset of samples. This insight encourages the development of adaptive guidance methods that address this issue and achieve more uniform performance gains, which is a potential practical application of our theory.''
**Influence of guidance scale $w$.**
We agree that extremely large values of $w$ can degrade the performance of CFG.
However, this phenomenon is consistent with both our theoretical and experimental results.
In practice, the performance of a diffusion model is typically evaluated based on two key metrics: diversity and sample quality. CFG attains a trade-off between these two metrics, as noted in [1]. In this paper, our main focus is on the influence of guidance on sample quality, particularly in relation to the Inception Score.
Our results align with practical observations in the sense that the generated samples are more closely adhere to the conditional distribution with larger $w$.
In addition, previous studies have shown that an extremely large $w$ can severely reduce sample diversity and negatively impact realism. While this is an important consideration for practical applications, it is not the main focus of this work.
We will add the following remark to avoid confusion:
''In practice, performance of diffusion models is commonly evaluated by two metrics: diversity and sample quality. This study primarily focuses on the sample quality measured in a similar way as the Inception Score, which increases with $w$. However, prior work [1] has demonstrated that large values of $w$ can significantly reduce sample diversity, leading to unsatisfactory performance in real-world applications.''
**Related works.**
Reference [4] proposed to use a bad version of the model for guiding diffusion models. We will cite it properly in our revision.
[1] Classifier-free Diffusion Guidance
[2] Rethinking the Inception Architecture for Computer Vision
[3] https://github.com/CompVis/latent-diffusion
[4] Guiding a Diffusion Model with a Bad Version of Itself
---
Rebuttal Comment 1.1:
Comment: Thanks for the author's reply. I'm keeping a positive rating.
---
Reply to Comment 1.1.1:
Comment: Thank you for your acknowledgment and for your efforts in reviewing our paper. We will revise the manuscript according to your suggestions. | null | null | null | null | null | null | null | null |
Directly Forecasting Belief for Reinforcement Learning with Delays | Accept (poster) | Summary: This paper addresses reinforcement learning with delayed observations by proposing a Directly Forecasting Belief Transformer (DFBT). DFBT treats state estimation as a sequence modeling problem—predicting the current (and intermediate) states directly from past delayed observations instead of forecasting them iteratively. The authors combine DFBT with Soft Actor-Critic and introduce multi-step bootstrapping from the predicted states to improve learning efficiency. Empirical results on MuJoCo tasks with both fixed and random delays show significantly higher performance than prior augmentation-based or recursively predicted belief methods.
## update after rebuttal
Both before and after the rebuttal phase, I believe that the work has a certain novelty, and therefore, I leave my current high assessment.
Claims And Evidence: The key claim is that direct (rather than recursive) forecasting mitigates compounding errors as delay increases, leading to superior policy returns. Their theoretical bounds show that the error does not scale exponentially with delays, and empirical comparisons on MuJoCo (e.g., HalfCheetah, Hopper, Walker2d) confirm much better performance at long delays. This is well-supported by both error metrics (on offline data) and final returns in the RL tasks.
One potential weakness is that DFBT requires an offline dataset to pre-train the belief model. In scenarios where such data is not available, one would have to gather it (possibly by random exploration) or train the model online (which the paper did not explore). Augmentation-based methods, by contrast, learn everything online (though at a heavy sample cost). The authors did not explicitly discuss this trade-off.
Methods And Evaluation Criteria: The authors pre-train the Transformer-based belief model using offline trajectories (D4RL) and then use it in online learning with a standard SAC agent. They measure belief prediction accuracy (L1/MSE error) and normalized returns on MuJoCo. Baselines include recent augmentation-based (BPQL, ADRL) and belief-based (D-SAC, D-Dreamer) methods, making the comparisons fair and thorough.
Theoretical Claims: They provide bounds showing that recursive belief estimation accumulates errors exponentially in the worst case, whereas direct prediction has a linear bound in terms of overall model error.
Experimental Designs Or Analyses: Experiments are methodically done on MuJoCo tasks with delays ranging from 8 to 128, as well as random delays.
Additional experiments that might make the paper stronger: 1. analyzing the impact of the algorithm for ood states 2. stochastic environment 3. Results for online finetuning the belief
Supplementary Material: The supplementary includes proofs, detailed hyperparameters, additional results (for different delay settings), and ablations.
Relation To Broader Scientific Literature: This work builds on both augmentation-based and belief-based delay handling methods, connecting to model-based RL (e.g., Dreamer) by learning a forward model but differs by predicting states in one shot with a Transformer.
Essential References Not Discussed: Works like TransDreamer (Chen et al., 2022) also explore Transformers in partially observable RL but from a full model-based viewpoint. Fu et al. also discusses compounding error bound with the Lipschitz assumption.
1. Reinforcement Learning with Transformer World Models. Chen et al.
2. Performance Bounds for Model and Policy Transfer in Hidden-parameter MDPs. Fu et al.
Other Strengths And Weaknesses: No
Other Comments Or Suggestions: Minor issues:
1. “delays are fundamentally affect the system’s safety”
2. “cypher-physical systems”
Questions For Authors: 1. How well does DFBT generalize if the policy visits out-of-distribution states not covered in the offline dataset?
2. Could fine-tuning the belief model online further boost performance or stability?
3. Have you considered outputting distributional beliefs for stochastic environments?*
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We sincerely appreciate Reviewer 4D3p's thoughtful comments. Our detailed responses to your questions and concerns are as follows:
>### Q1: One potential weakness is that DFBT requires an offline dataset to pre-train the belief model. In scenarios where such data is not available, one would have to gather it (possibly by random exploration) or train the model online (which the paper did not explore). Augmentation-based methods, by contrast, learn everything online (though at a heavy sample cost). The authors did not explicitly discuss this trade-off.
Thanks for your insightful comment on the trade-off between augmentation-based and belief-based approaches. We will add the related discussion in the revised paper based on your suggestion. As mentioned in the paper (Lines 406-411), learning DFBT online from scratch always suffers from instability and inefficacy issues. Therefore, we separate the belief learning from the RL process for stabilizing the online learning process. Separating belief learning from the online RL process and freezing belief representation during RL allows us to investigate the belief component solely, eliminate potential influences from the RL side. To address the reviewer's concern, we report the experimental results of learning belief representation on MuJoCo tasks with deterministic 32 delays in Table R4. The results show that directly learning belief representation in the RL process suffers from instability and efficiency, thus leading to poor performance.
>### Q2: How well does DFBT generalize if the policy visits out-of-distribution states not covered in the offline dataset? Could fine-tuning the belief model online further boost performance or stability?
Thanks for the thoughtful suggestions. In the online RL process, the agent indeed visits out-of-distribution (ood) states, which leads to a relatively limited performance gain. As mentioned by the reviewer, this issue can be addressed by fine-tuning the belief representation with the online RL process. To address this concern, we conduct the additional experiment: fine-tuning DFBT online on MuJoCo tasks with deterministic 32 delays. The experimental results show that fine-tuning the belief representation can gain better performance improvement with much longer training hours (increasing training hours from 6 to 12). Note that there are other methods to improve the DFBT's online performance. However, they are orthogonal to this work's contribution. Therefore, in this paper, we separate belief learning from the online learning process, which allows us to investigate the belief component solely, eliminate potential influences from the RL side. We will add related discussions in the revised version.
Table R4. Performance comparison of fixed and fine-tuned DFBT on MuJoCo tasks with deterministic 32 delays.
|Task|Online|Offline|Offline + Fine-tuning|
|--|--|--|--|
|HalfCheetah-v2|$0.11\pm0.39$|$\mathbf{0.42\pm0.12}$|$0.39\pm0.04$|
|Hopper-v2|$0.10\pm0.58$|$0.68\pm0.20$|$\mathbf{0.84\pm0.04}$|
|Walker2d-v2|$0.09\pm0.27$|$0.64\pm0.10$|$\mathbf{0.96\pm0.32}$|
>### Q3: Have you considered outputting distributional beliefs for stochastic environments?
Thanks for the helpful suggestions. We conducted additional experiments on the stochastic MuJoCo tasks with a probability of 0.001 for the unaware noise (similar settings with related works [1, 2]) and deterministic 128 delays. As shown in Table R5, the results demonstrate that our DFBT-SAC with distributional belief achieves superior performance in these stochastic MuJoCo tasks.
Table R5. Performance on stochastic MuJoCo with deterministic 128 delays.
|Task|A-SAC|BPQL|ADRL|DATS|D-Dreamer|D-SAC|DFBT-SAC|
|--|--|--|--|--|--|--|--|
|HalfCheetah-v2|$0.00\pm0.03$|$0.01\pm0.05$|$0.13\pm0.04$|$0.13\pm0.03$|$0.07\pm0.01$|$0.00\pm0.04$|$\mathbf{0.35\pm 0.04}$|
|Hopper-v2|$0.03\pm0.04$|$0.08\pm0.05$|$0.06\pm0.04$|$0.05\pm0.06$|$0.04\pm0.05$|$0.04\pm0.05$|$\mathbf{0.13\pm 0.22}$|
|Walker2d-v2|$0.06\pm0.02$|$0.04\pm0.01$|$0.08\pm0.01$|$0.06\pm0.03$|$0.10\pm0.03$|$0.05\pm0.02$|$\mathbf{0.30\pm 0.07}$|
>### Q4: Works like TransDreamer (Chen et al., 2022) also explore Transformers in partially observable RL but from a full model-based viewpoint. Fu et al. also discusses compounding error bound with the Lipschitz assumption.
Thanks for the suggestions on missing related works. We will discuss these related works and references in the revised paper.
>### Q5: Minor issues: "delays are fundamentally affect the system’s safety" and "cypher-physical systems"
Thanks for your helpful comments. We will fix these typos in the revised version.
>### Reference
>[1] Kim, Jangwon, et al. "Belief projection-based reinforcement learning for environments with delayed feedback." Advances in Neural Information Processing Systems.
>
>[2] Wu, Qingyuan, et al. "Boosting Reinforcement Learning with Strongly Delayed Feedback Through Auxiliary Short Delays." International Conference on Machine Learning. | Summary: This paper introduces a method for directly predicting the current belief state in reinforcement learning with delays using a Transformer-based model. The main idea is to use Transformers for state forecasting to help mitigate the effects of observation delays in RL environments. The approach is simple, modular, and easy to implement.
Claims And Evidence: 1. Performance claims are well-supported by comprehensive experiments across delay settings.
2. Ablation studies on multi-step bootstrapping provide convincing evidence of this technique's importance.
3. Innovation claim somewhat overstated - direct prediction approach itself isn't new when handling delay problem in RL.
Methods And Evaluation Criteria: 1. The proposed method is based on a Transformer architecture for belief forecasting, which is intuitive and straightforward.
2. The experimental setup considers high delays (8 to 128 steps) and random delays (U(1,n) distribution), making the evaluation more aligned with real-world scenarios.
However:
1. The separation of the prediction module from the reinforcement learning process limits the ability of the prediction network to adapt to task-specific informations. This design choice could lead to inefficiencies in tasks where task-relevant information differs from state prediction accuracy.
2. The choice to operate directly in the original state space may lead to inefficiencies in high-dimensional environments. The decision to predict directly in the original state space rather than learning a task-optimized lower-dimensional representation presents challenges in high-dimensional environments. This approach risks the "curse of dimensionality" when states contain redundant or task-irrelevant information. In complex environments, only a subset of state variables may be critical for decision-making, making direct prediction of the entire state inefficient. A comparison with approaches that learn low-dimensional task-specific representations could provide additional insights.
Theoretical Claims: No special points to be mentioned.
Experimental Designs Or Analyses: 1. Methodology appropriate for research problem, using standard experiments for delays. It covers motion controlling, would be great if it can be extended to other areas.
2. Good testing across environments with different delay characteristics such as randomness and time scale.
3. Well-designed ablation studies, such as bootstrapping steps (N=1,2,4,8).
To be improved:
The direct prediction approach likely offers computational advantages over complex recursive forecasting methods. By avoiding intermediate steps, it reduces error accumulation and computational overhead. An explicit analysis of computational efficiency (training time, inference speed, memory usage) would strengthen the paper's practical value proposition.
Supplementary Material: I did review the supplementary material roughly.
Relation To Broader Scientific Literature: While the paper's conceptual innovation may be limited, its main contribution lies in providing an efficient, straightforward, and universally applicable solution to the delayed reinforcement learning problem using modern frameworks. Although the core ideas have appeared in previous methods, the paper's implementation using contemporary Transformer architecture brings practical improvements. The significance of this work is not in proposing entirely new concepts, but in effectively adapting modern deep learning techniques to create an "out-of-the-box" solution that outperforms existing approaches.
Essential References Not Discussed: N/A.
Other Strengths And Weaknesses: See above
Other Comments Or Suggestions: See above
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate Reviewer dQtK's thoughtful comments. Below, we give responses to your questions and concerns.
>### Q1: Contribution and Novelty Clarification
First, we would like to express our gratitude for the reviewer's comments. We recognize that our current statement may have led to some misunderstandings, and we will refine the claim and clarify the statement in the revised version. Here, we want to clarify our contribution and the novelty. This paper aims to address the compounding errors issue in belief-based methods via directly forecasting belief. While we acknowledge that the directly forecasting approach has been used in delayed RL, and we have cited the related work and considered it as the baseline [1], we note that existing work with online belief learning always suffers from instability and inefficacy issues. To overcome these issues, we separate the belief training from the RL process to stabilize the online learning process (Lines 406-411). Specifically, as shown in Fig. 1, the DFBT is trained on the offline datasets, then later frozen and deployed in the environment with delays, enabling efficient RL training. To this end,
1. We propose DFBT, which incorporates reward signals in tokens for capturing sufficient dynamic information. Empirical results (Fig. 2) demonstrate that DFBT achieves superior prediction accuracy, effectively addressing the compounding errors issue.
2. By leveraging the accurate predictions from DFBT, we integrate the multi-step bootstrapping technique on the forecasted states to improve learning efficiency.
3. We theoretically demonstrate that directly forecasting belief significantly mitigates compounding errors, providing a stronger performance guarantee.
>### Q2: The separated belief is limited to task-specific information of RL.
We acknowledge that some task-specific information may be missing if the belief is frozen in the RL process, leading to limited performance improvement. This issue can be mitigated by fine-tuning the belief within the RL process. The results, shown in Table R2, demonstrate that fine-tuning helps the DFBT capture the task-specific information with better performance. Note that there are many potential methods for capturing task-specific information not limited to fine-tuning DFBT. However, they are orthogonal to this work's contribution. We will add related discussions for broader interests in the revised version. As mentioned in the limitations (Lines 406-411), belief learning from scratch in the online RL process always suffers from instability issues. Therefore, in this paper, we separate belief learning from the online RL process, which allows us to investigate the belief component solely, eliminate potential influences from the RL side.
Table R2. Performance comparison of DFBT-SAC with different training methods on MuJoCo tasks with 32 delays.
|Task|Online|Offline|Offline + Fine-tuning|
|--|--|--|--|
|HalfCheetah-v2|$0.11\pm0.39$|$\mathbf{0.42\pm0.12}$|$0.39\pm0.04$|
|Hopper-v2|$0.10\pm0.58$|$0.68\pm0.20$|$\mathbf{0.84\pm0.04}$|
|Walker2d-v2|$0.09\pm0.27$|$0.64\pm0.10$|$\mathbf{0.96\pm0.32}$|
>### Q3: Inefficiencies in high-dimensional environments.
In this work, we mainly consider MuJoCo tasks, which have relatively low-dimensional state spaces, such as HalfCheetah (17), Hopper (11), and Walker2d (17). As discussed in the paper (Lines 47-51, 99-102), our approach belongs to the belief-based method, which can efficiently address the "curse of dimensionality" issue of the augmentation-based approach in facing long delays. For the high-dimensional state space (e.g., image-based RL tasks), it is essential to learn a low-dimensional and compact latent state space for efficient state prediction. However, this falls outside the scope of the current paper. We will include a related discussion in the revised version and plan to explore high-dimensional delayed RL tasks in future work.
>### Q4: Experiments on computational efficiency.
Thanks for your helpful suggestion. Based on your advice, we conducted additional computational efficiency experiments. As shown in Table R3, the results demonstrate that directly forecasting belief maintains a consistent and stable inference speed (around 4 ms) across different delays. In contrast, the recursively forecasting belief experiences inference speed issues as delays increase. In HalfCheetah-v2 with 128 delays, the training times of DATS and D-Dreamer are around 10 hours and 15 hours, respectively, while that of D-SAC and DFBT-SAC both are around 6 hours.
Table R3. Inference speed (ms) comparison in HalfCheetah-v2.
|Delays|DATS|D-Dreamer|D-SAC|DFBT-SAC|
|--|--|--|--|--|
|8|$1.10\pm0.02$|$1.85\pm0.01$|$4.03\pm0.03$|$4.18\pm0.04$|
|32|$3.85\pm0.06$|$6.80\pm0.04$|$4.03\pm0.04$|$4.18\pm0.04$|
|128|$14.97\pm0.22$|$26.51\pm0.19$|$4.03\pm0.03$|$4.15\pm0.05$|
>### Reference
>
>[1] Liotet, Pierre, et al. "Learning a belief representation for delayed reinforcement learning". | Summary: The authors focus on reinforcement learning with delayed observations. To mitigate this issue, most prior work learns a dynamics model which, given a known delay time $\Delta t$, rolls out a dynamics model from $t$ to $t + \Delta t$. The policy then makes decisions based on $s_{t + \Delta t}.
While prior work tends to use recurrent models, the authors suggest using a transformer to generate all states between $s_t$ and $s_{t + \Delta t}$ in one shot, sidestepping error propagation that might occur from calling a recurrent model sequentially.
The authors train their transformer to predict future states using the negative log likelihood. They pretrain their transformer on offline dataset, then freeze the parameters and utilize the transformer-produced states to train the policy and value function as one would in normal RL.
The authors provide some error bounds for belief forecasting, then run some experiments on MuJoCo tasks. First, they plot the belief forecasting error, and then they compare the corresponding trained policy performance
Claims And Evidence: The authors claim to:
- Propose a transformer architecture to tackle the forecasting problem
- Integrate the architecture in SAC
- Demonstrate that their method reduces compounding forecasting errors
- Demonstate that their method results in better policies
I think they provide sufficient evidence to back their claims.
Methods And Evaluation Criteria: The authors select a standard MuJoCo baseline, however they only focus on three tasks. I think it could be helpful to evaluate on the entire MuJoCo suite, even if the other results are only written in the appendix.
Theoretical Claims: The authors make theoretical claims but I did not check them closely.
Experimental Designs Or Analyses: The experimental design consists of both deterministic and random delays, and performs ablations.
I commend the authors for also demonstrating the DFBT-SAC(1) results. Initially, I was concerned that their improved returns could result primarily from the use of an n-step return. This ablation assuages my concerns.
Supplementary Material: I looked at the appendix but not in detail.
Relation To Broader Scientific Literature: I an not familiar with the field of delayed RL.
Essential References Not Discussed: I an not familiar with the field of delayed RL.
Other Strengths And Weaknesses: The authors' method is well-founded and their experimental setup is well-done. The idea is fairly straightforward and provides strong results.
I think the writing could be a bit clearer, and I suggest the authors go through the paper and try to minimize tense changes and stick to either passive or active voice.
My biggest concern is not necessarily on the authors work, but rather with the field of "delayed RL". I suspect that most realistic robotics tasks already integrate an RNN/Transformer to handle partial observability. Such a setup would be able to handle delayed observation-action interactions implicitly, removing the need to consider delayed RL as a separate problem.
Other Comments Or Suggestions: As above, try and be more consistent with grammatical tense and voice to make the paper slightly nicer to read. More MuJoCo tasks could also strengthen the evidence for the authors' claims.
Questions For Authors: It is unclear to me why the transformer architecture works so much better for stochastic delays. For $U(1, 128)$, does this just mean learning a deterministic delay of $64$? If you cannot know the delay ahead of time, it seems like this is the best you can do. Can you explain this further?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: We sincerely appreciate Reviewer KEME's thoughtful comments. Below, we give responses to your questions and concerns.
>### Q1: Evaluation of other MuJoCo tasks.
In this work, we consider the MuJoCo benchmark. To ensure transparency and reproducibility in belief training, we utilize the open offline RL datasets (D4RL), including HalfCheetah-v2, Hopper-v2, and Walker2d-v2 only. We acknowledge that other tasks are also valuable. Therefore, we conducted experiments on the Pusher-v2, Reacher-v2, and Swimmer-v2 with deterministic 32 delays. The offline datasets (500k samples) are collected from a SAC policy, with other settings unchanged. The results are shown in Table R1, showing that DFBT-SAC achieves superior performance on these tasks.
Table R1. Performance on additional tasks with deterministic 32 delays.
|Task|A-SAC|BPQL|ADRL|DATS|D-Dreamer|D-SAC|DFBT-SAC|
|--|--|--|--|--|--|--|--|
|Pusher-v2|$0.05\pm 0.00$|$0.93\pm 0.58$|$0.95\pm 0.24$|$0.92\pm 0.10$|$0.87\pm 0.18$|$0.94\pm 0.04$|$\mathbf{1.04\pm 0.24}$|
|Reacher-v2|$0.89\pm 0.08$|$0.83\pm 0.06$|$0.85\pm 0.01$|$0.82\pm 0.13$|$0.84\pm 0.02$|$0.88\pm 0.07$|$\mathbf{0.93\pm 0.06}$|
|Swimmer-v2|$0.27\pm 0.05$|$0.80\pm 0.14$|$0.60\pm 0.06$|$0.25\pm 0.05$|$0.21\pm 0.07$|$0.30\pm 0.07$|$\mathbf{1.01\pm 0.27}$|
>### Q2: Writing and grammar issues.
Thanks for the reviewer's helpful suggestions. We will revise the paper to improve clarity and ensure consistency in grammatical tense and voice.
>### Q3: Necessity of treating "delayed RL" as a separate research problem.
As the reviewer mentioned, some robotics tasks incorporate RNN or Transformer to handle partial observability. We acknowledge that these models implicitly address delays by capturing sequential dependencies and retaining memory over time. However, we emphasize that **explicitly handling delayed observation-action interactions through delayed RL remains essential both technique-wise and application-wise**. The key reasons are as follows:
(1) **Unique problem structure enables specialized algorithms.** Delayed MDP poses unique challenges due to entirely missing observations rather than partially missing ones, though it can be viewed as a specialized form of POMDP [1]. **Its explicit delay-induced structure enables specialized, efficient algorithms that outperform general-purpose POMDP methods**. For example, at timestep $t$, the agent can only access the historical state $s_{t-\Delta}$. In this context, the agent has to explicitly handle delays $\Delta$ using state augmentation [2] or belief representation [3] techniques to retrieve the Markovian property and enable efficient RL. For instance, in the state augmentation technique, the decision-making is based on the augmented state $x_t:=\\{s_{t-\Delta},a_{t-\Delta:t-1}\\}$. This paper aims to address the compounding errors issue within the belief representation method, thereby enhancing learning efficiency and performance. These distinctive properties and challenges in delayed RL necessitate treating it as a distinct research problem, separate from the conventional partially observable RL problem.
(2) **Strong application-driven motivations.** Delayed RL aims to address the delayed feedback problem, which is practical and common in real-world control applications (e.g., transportation systems [4] and financial systems [5]). In robotics, several studies have demonstrated that delayed RL could improve the system's safety, agility, efficiency, and robustness [6, 7]. The practical demands of real-world scenarios also underscore the necessity to investigate delayed RL as a distinct research problem.
>### Q4: $U(1, 128)$ delays explanation and Transformer for stochastic delays.
For $U(1, 128)$ delays, it does not mean learning the deterministic delays of $64$. Under this setting, in each timestep $t$, the probability of observed state $s_{t-1}$ equals that of every observed state till $s_{t-128}$. Therefore, the agent shall have the ability to address varying delays ranging from 1 to 128. As shown in Fig.2, the transformer can effectively address the compounding errors issue, maintaining superior and consistent prediction accuracy across varying delays. These accurate predictions further improve the learning efficiency and final performance of RL.
>### Reference
>
>[1] Karamzade, Armin, et al. "Reinforcement learning from delayed observations via world models".
>
>[2] Bouteiller, Yann, et al. "Reinforcement learning with random delays".
>
>[3] Walsh, Thomas J., et al. "Learning and planning in environments with delayed feedback".
>
>[4] Cao, Zhiguang, et al. "Using reinforcement learning to minimize the probability of delay occurrence in transportation".
>
>[5] Deng, Yue, et al. "Deep direct reinforcement learning for financial signal representation and trading".
>
>[6] Mahmood, A. Rupam, et al. "Setting up a reinforcement learning task with a real-world robot".
>
>[7] Hwangbo, Jemin, et al. "Control of a quadrotor with reinforcement learning". | null | null | null | null | null | null | null | null |
The Role of Sparsity for Length Generalization in LLMs | Accept (poster) | Summary: This work suggests that length generalization occurs as long as each predicted token depends on a small (fixed) number of previous tokens. This work also conducts experiments on synthetic tasks and natural language.
Claims And Evidence: Yes, the experiment results support the claims and evidence
Methods And Evaluation Criteria: Yes, the syntheic task and nature language part results make sense.
Theoretical Claims: I have checked the proofs.
Experimental Designs Or Analyses: I have checked the soundness/validity of experimental designs and analyses
Supplementary Material: I have read the Appendix
Relation To Broader Scientific Literature: This work finds that length generalization occurs as long as each predicted token depends on a small (fixed) number of previous tokens.
Essential References Not Discussed: It seems that the key contribution is not new, which is discussed in the following:
[1] Fang, L., Wang, Y., Liu, Z., Zhang, C., Jegelka, S., Gao, J., ... & Wang, Y. (2024). What is Wrong with Perplexity for Long-context Language Modeling?. arXiv preprint arXiv:2410.23771.
[2] Zheng, C., Gao, Y., Shi, H., Xiong, J., Sun, J., Li, J., ... & Li, Y. (2024). DAPE V2: Process Attention Score as Feature Map for Length Extrapolation. arXiv preprint arXiv:2410.04798.
Other Strengths And Weaknesses: Weakness:
* The key contribution of the work is that length generalization occurs as long as each predicted token depends on a small (fixed) number of previous tokens. **However, it seems that the contribution is not new**, and it has already been discussed in the previous works [1,2]. Therefore, the author should clearly provide the difference between this work and previous work [1,2]
* Also, the core method, presented in Figure 6, is just the sparse attention, which is well-discussed in previous works [3,4].
* Therefore, the author should clearly distinguish their contribution with the previous works.
[1] Press, O., Smith, N. A., & Lewis, M. (2021). Train short, test long: Attention with linear biases enables input length extrapolation. arXiv preprint arXiv:2108.12409.
[2] Fang, L., Wang, Y., Liu, Z., Zhang, C., Jegelka, S., Gao, J., ... & Wang, Y. (2024). What is Wrong with Perplexity for Long-context Language Modeling?. arXiv preprint arXiv:2410.23771.
[3] Ma, X., Liu, Y., Liu, J., & Ma, X. (2025). Mesa-Extrapolation: A Weave Position Encoding Method for Enhanced Extrapolation in LLMs. Advances in Neural Information Processing Systems, 37, 81389-81436.
[4] Lou, C., Jia, Z., Zheng, Z., & Tu, K. (2024). Sparser is faster and less is more: Efficient sparse attention for long-range transformers. arXiv preprint arXiv:2406.16747.
Other Comments Or Suggestions: N/A
Questions For Authors: The key contribution of the work is not new and has already been discussed in previous works. The authors have to give a response to such limitation.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your comments. Below we contrast our work to each of the papers you mentioned. We want to emphasize that with the exception of the 4th paper below (whose theory is different from ours), none of them provide any theoretical analysis, unlike our paper. Moreover, we wish to emphasize that our core method is neither presented in Figure 6 nor is sparse attention. Rather, our main contribution is to explain, using both theory and experiments, why having a sparse dependency structure in data can allow length generalization. We also note that it does not appear that the experiment presented in Figures 2 \& 6 is present in any of the papers you pointed out.
1. *``What is Wrong with Perplexity for Long-context Language Modeling?''* While the quantity $LSD_\theta(x_i)$ from this paper (which measures the difference in log-likelihoods of the current token using long and short context windows, and is essentially equivalent to what we call $L_{{long}} - {L}_{{short}}$) also plays a role in our paper, a key aspect of our experimental results is that of the tokens in the longer context window, a small number of them can be used to predict the current token $x_i$ nearly as well as all of the long-distance tokens. This ``sparse dependency pattern'' is not highlighted in this prior work.
2. *``DAPE V2: Process Attention Score as Feature Map for Length Extrapolation.''* While the main method proposed in this paper, DAPE, may be motivated by similar considerations regarding the sparse dependency structure of many tasks (such as associative recall), we emphasize that the content of this paper, which proposes a new empirical method based on applying an MLP to attention patterns so as to improve length extrapolation, is entirely different from ours.
3. *``Train short, test long: Attention with linear biases enables input length extrapolation.''* We already cite this paper (which introduces ALiBi). We would like to highlight one key difference between our message and that of the ALiBi paper: whereas ALiBi biases the model to put less attention on tokens far in the past, one of our main messages is that length generalization can occur in the (orthogonal) situation when the current token depends on a small number of tokens far in the past.
4. *``Mesa-Extrapolation: A Weave Position Encoding Method for Enhanced Extrapolation in LLMs.''* This paper has some theoretical analysis showing that certain transformers which fail to length extrapolate for NoPE or ALiBi can length extrapolate for some modified positional encoding schemes introduced therein (namely, Weave PE Extrapolation and Mesa Extrapolation), as well as supporting experiments. These contributions are entirely different from our own.
5. *``Sparser is faster and less is more: Efficient sparse attention for long-range transformers.''* Using sparse attention, as proposed in this paper, may be motivated by observing that the attention patterns of many actual transformers is sparse, which is closely related to the sparse dependency structure in the data which is the main focus of our paper. Nevertheless, our contribution is *not* to (re-)introduce sparse attention, but rather explain why such a sparse dependency structure suffices for length extrapolation using both theory and experiments. | Summary: This paper studies why LLMs sometimes can or cannot generalize to input sequences longer than those they were trained on. The authors propose a theoretical framework centered on the concept of "sparsity": the idea that good length generalization occurs when each predicted token depends on only a small, fixed number of previous tokens rather than the entire context.
The paper shows that "locality" (tokens being close together) is also important for length generalization, but this requirement can be mitigated using position coupling techniques, and it introduces "Predictive Position Coupling", an extension of position coupling that allows the model to predict the position IDs for tokens dynamically rather than having them fixed.
Claims And Evidence: The claim that natural language exhibits the sparse planted correlation property is only partially demonstrated. Their experiments show promising evidence, but a more comprehensive analysis of different types of linguistic dependencies and their relationship to length generalization would be needed to fully support this claim.
Methods And Evaluation Criteria: The proposed methods and evaluation criteria seem sound.
Theoretical Claims: - Definition 3.2 (k-sparse planted correlations) - the assumption that non-relevant tokens are i.i.d. from a background distribution is acknowledged as unrealistic. This simplification might affect how well the theory translates to real-world language data.
Experimental Designs Or Analyses: - The paper doesn't fully explain how the "k influential tokens" in the natural language experiments are selected. This is crucial for interpreting the results in Figure 2.
- The experiments don't thoroughly explore how the relationship between sparsity and length generalization might change with model scale, which is important for practical applications.
- While the paper includes confidence intervals for synthetic tasks, a more thorough statistical analysis would strengthen the conclusions, particularly for the natural language experiments.
Supplementary Material: I quickly read the appendix.
Relation To Broader Scientific Literature: In the broader landscape of LLM research, this paper helps bridge the gap between the theoretical understanding of transformers and practical techniques for improving their capabilities, particularly regarding handling long contexts efficiently.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: other strenghts:
- The introduction of Predictive Position Coupling is an important contribution that extends position coupling to more general settings where the mapping between positions is input-dependent. This broadens the applicability of position coupling techniques.
- The findings have clear practical implications for designing models that generalize better to longer sequences, suggesting that architectures encouraging sparse dependencies might perform better in length generalization tasks
Other weaknesses:
- While the paper includes experiments on natural language data, this section is less developed than the synthetic task experiments. The measurement of sparsity in natural language contexts could be more thorough, with more detailed analysis of how different types of linguistic dependencies affect length generalization.
Other Comments Or Suggestions: this is just a suggestion, but i personally find a bit uncomfortable to read the paper given that all the references are in a very bright blue. i'd suggest changing the color in a less bright one.
Questions For Authors: N/A
Ethical Review Concerns: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your positive comments!
Regarding the how the $k$ influential tokens are chosen: please see the discussion around Eq.~(20) in the appendix.
---
Rebuttal Comment 1.1:
Comment: I thank the authors and after reading their response i decided to keep my overall score to 4. | Summary: This work mathematically studies the context length generalization for a single next-token prediction task. It obtains a length generalization error upper bound when the task satisfies certain sparsity (i.e., only a subset of tokens in a context is important to solve the task), locality (i.e., the important tokens must be close to each other), and regularity (i.e., distributions of important token positions do not change a lot with respect to the context length). While locality might be difficult to be satisfied for general next-token prediction tasks, this work also shows that a task-specific position ID re-assignment, Position Coupling, can resolve the issue.
On the empirical side, first, the general theoretical findings (without position coupling technique) are verified on the sparse parity task. To develop the idea of position coupling and mitigate its limitation, a variant called Predictive Position Coupling (PPC) is proposed; the efficacy of PPC is tested for parity (with scratchpad) task and variable assignment task. Lastly, the interplay between sparsity and length generalization capability is studied for the natural language dataset.
Claims And Evidence: The theoretical claims (mainly, Theorem 4.3 and Proposition 4.4) are clearly supported by their proofs provided in Appendices C and D. The authors’ main insight is also tested by several experiments. However a particular claim that “PPC relaxes the downside of position coupling” doesn’t seem to be well supported by any evidence because of lack of PPC’s implementation details: I hope to see a (sub-)section of appendix dedicated to more detailed descriptions about the implementation, training, and evaluation methods using PPC.
Methods And Evaluation Criteria: The paper has chosen several appropriate tasks to examine and verify their claim about crucial factors in achieving length generalization.
Theoretical Claims: I checked almost every math in all proofs. Most of them seem “correct”, but I mainly am worried about the significance (or tightness) of the given error bound. Below, I list all my concerns about the theoretical parts of the paper.
- The $L$ factor in the bound looks like appearing due to the very first step of the proof: when bounding the risk of $\hat{h}$ for trained lengths $\ell \le L$ by $L\delta$. This seems like an artifact of the analysis, especially caused by $\hat{h}$ defined with an argmin of an expectation. Why don’t we re-define it as a minimax-type estimator, to consider the case where the in-distribution (ID) generalization is already done quite well? For example: $\hat{h} = \arg\min\_{h\in \mathcal{H}} \max\_{\ell\in [L/2, L]} \mathbb{E}\_{({\bf X},{\bf Y})\sim P\_\ell} [\mathcal{L}(h({\bf X}),{\bf Y})].$ In this case, we have a $\delta$-bound instead of $L\delta$-bound:
$$
\begin{align*} \mathbb{E}\_{({\bf X},{\bf Y})\sim P\_\ell} [\mathcal{L}(\hat{h}({\bf X}),{\bf Y})] &\le \max\_{\ell'\in [L/2, L]} \mathbb{E}\_{({\bf X},{\bf Y})\sim P\_{\ell'}} [\mathcal{L}(\hat{h}({\bf X}),{\bf Y})] \\\\ &\le \max_{\ell'\in [L/2, L]} \mathbb{E}\_{({\bf X},{\bf Y})\sim P\_{\ell'}} [\mathcal{L}(h^\star({\bf X}),{\bf Y})] \\\\ &\le \delta.\end{align*}
$$
I am a bit concerned about the $L$ factor because the current theorem tries to claim that the error bound may increase as we elongate the trained sequences. It is quite opposite to a common empirical observation that the length generalization capability grows as we train a model on longer sequences. But good news, this issue might be able to be relaxed with a different definition of $\hat{h}$! Still, the parameter $\eta_L$ may scale with $L$ in worst case, so the problem is not completely gone.
- I don’t think the regularity assumption (Ass. 4.2) immediately implies, together with Def 3.2, that the density ratio bounds in math equations roughly in line 885, which is just above Equation (5). I’d be happy if a slightly more detailed derivation is shown in the proof (like in Equation (10)).
- Typo: In a math equation (see line 885; above Equation (5)), $\mathcal{P}_{L-L_{\sf local}}(\mathbf{X}_{1:L-L_{\sf local}}, S^{\star})$ seems correct.
- There seem to be several errors in indices, especially after Equation (8): $t_0 + t_1$ or $t_0+t_1+2$?
- I don’t think the risk bound provides any useful insight about the $L_{\sf local}$-dependency. By merely following the proof, it seems that the error bound is proportional to $(\bar{L} / L_{\sf local})^2$. But is that all? I don’t think so, because it is difficult to understand that the length generalization capability may degrade as the locality gets better (i.e., $L_{\sf local}$ gets smaller). In fact, $\eta_{\bar{L}}$ also depends on $L_{\sf local}$. In my opinion, the theoretical analysis can be stronger by providing an appropriate discussion regarding these.
- One of my biggest concern is the scale of $\eta_{\bar{L}}$. It can be extremely large as it bounds the ratio between two distributions relevant to a very short context length (namely, $L-2L_{\sf local}$) and a large one (namely, $\bar{L}$). If this is the case, can we say that the provided error bound is not vacuous?
- Moving on to the necessity of assumptions (Appendix C.2): I guess the “provable necessity” of the introduced assumptions is an over-claiming since Appendix C.2 does not guarantee that we will fail to discuss length generalizability **every time** we violate one of them. A tone-downed claim might work.
- Minor comment in Def 3.3: I guess $\mathbb{N}^k\times \mathcal{V}^k$ is correct, instead of $(\mathbb{N}\times \mathcal{V})^k$.
Experimental Designs Or Analyses: I checked the experimental designs and their results. The experiments mostly support the main insight of the paper well, while missing some minor details or discussions.
- I can’t find whether PPC doesn’t require the task structure at all. Does the proposed method never require the coupled position IDs in test time? How about in training time? Moreover, doesn’t the training on the prediction of coupled position IDs cause an additional axis of length generalization? If it does, why does the position ID prediction work well even at evaluation time, while the prediction of new next position ID might depend on every previously assigned position IDs (which does not seem to be a ‘sparse’ task)?
- Although not being a *necessary* analysis, “Needle in a Haystack” benchmark might be an extreme case where the authors’ claim should hold. However, they did not discuss the relationship between this task and their claim in the paper. Note that, in fact, several LLMs fail in this benchmark.
Supplementary Material: N/A
Relation To Broader Scientific Literature: The key contribution of this work is highly related to scaling up the sequence-to-sequence models (like language models based on decoder-only Transformers).
Essential References Not Discussed: I can’t find any missing essential references.
Other Strengths And Weaknesses: **Strengths**
- I love the paper explaining why position coupling can improve length generalization; it removes the necessity of locality assumption, allowing more tasks to be length-generalizable. It aligns well with the intuition on the benefit of position coupling explained in Cho et al (2024b), adding mathematical rigor significantly.
**Weaknesses**
- The relativity of the class $\mathcal{G}^{\sf key}$ is a bit confusing. In case of $k=1$, the definition of relativity will assign the same attention score to every token; is this realistic? Also, I hope the paper will explain more clearly about why the Item 2 of Assumption 3.2 models the usage of “relative position information”.
- Be consistent with the jargon: there are both “position coupling” and “positional coupling” in the main text. It’d be better to choose only one of them.
Other Comments Or Suggestions: See above.
Questions For Authors: Authors can find my questions above (sorry for not numbering them…). I am willing to update my evaluation if all the concerns get resolved.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your helpful feedback!
**Regarding the various $L$ factors.** Thank you for these great insights that allow us to improve our bounds!
Though we did not attempt to optimize these factors in our submission, as you point out, one can indeed improve the dependence on $L$ and $\bar L$, which we discuss in further detail below in response to your questions.
(For the purpose of interpreting our theoretical results as stated currently, one can think of $\bar L = O(L), \eta_L = O(L), \eta_{\bar L} = O(\bar L)$ (see Remark C.1), and $\delta \leq o(L^{-5})$, which implies a length generalization error (per Theorem 4.3) of $o(1)$.)
- Yes, the factor of $L$ in the error bound can be removed by adopting a minimax objective, as you suggest. (We remark that the objective in Eq.~(3) aligns more closely with what is done in practice, which is to mix over a range of context lengths during training.)
- Yes, the factor of $\bar L^2$ in the error bound can be replaced with $(\bar L / L_{{local}})^2$. The intuition here is that the proof is using $L_{local}$-locality to incorporate the longer context in ``chunks'' of size $L_{local}$. Since there is added error each time we add a chunk, the overall error will scale with $\bar L/L_{local}$. Thus, to minimize the error we want to maximize the size of the chunks. The largest possible value of $L_{local}$ which still satisfies the assumption of the theorem statement is $L_{local} = L/4$; by choosing this value of $L_{local}$, we can further improve the error dependence to $O((\bar L / L)^2)$. (Essentially, the current counterintuitive bound occurs because the technique used in the proof with values $L_{local} < L/4$ is a suboptimal approach to bound the error, which becomes less suboptimal as $L_{local}$ increases).
- Regarding the size of the parameters $\eta_L, \eta_{\bar L}$, please see Remark C.1, which gives reasonable conditions under which we have $\eta_\ell = O(\ell)$ for all $\ell$. Note that, for a fixed choice of distributions $Q_\ell^{pos}$, increasing the parameter $L_{local}$ can only make it easier to satisfy Assumption 4.2 for a given choice of $\eta_{\ell}$. (That said, if we maximize over distributions $Q_\ell^{pos}$ supported on sets $S^\star$ of a given locality $L_{local}$, then the worst-case value of $\eta_\ell$ may increase with increasing values of $L_{local}$.)
- We remark that the dependence on $\eta_L, \eta_{\bar L}$ in the overall error bound of Theorem 4.3 can also be removed under appropriate assumptions: for instance, if we make the distributional assumption of Remark C.1, then the instance of $\eta_L$ in Line 885 can be replaced with $O(1)$ since it is comparing between lengths $L$ and $L - 2L_{local} \geq L/2$. Under the same assumption, the instance of $\eta_{\bar L}$ in Eq.~(10) can also be replaced with $O(1)$ since it is comparing between lengths $\bar L$ and $L - 2L_{local}$; the former length $\bar L$ is larger and on the numerator, meaning that the distribution $Q_{\bar L}^{pos}$ is more ``spread out'' and will put less mass on any $S^\star$ under the assumption in Remark C.1.
- Summarizing, if we incorporate all of the optimizations discussed above, we can decrease our overall error bound from $O(\eta_L \eta_{\bar L} L \bar L^2 \cdot \delta)$ to $O((\bar L / L)^2 \cdot \delta)$, which does not decay with $L$. Hopefully this addresses your concern. We will update the paper to incorporate this discussion.
- We will add more details surrounding the equation around line 885.
**Regarding details of PPC.** The description of PPC can be found on page 7, though we will add a more detailed description. To answer your questions: when discussing PPC, we distinguish between the prompt and the response. During training time, the coupled position IDs for both prompt tokens and response tokens are fed to the model, and the model is trained to predict the coupled position IDs for the response tokens (as well as the actual response tokens). During testing time, the coupled position IDs are only needed for the prompt tokens, but not the response tokens (the model will predict the coupled position IDs for the response tokens).
Yes, training the model to predict position IDs adds an additional axis of length generalization. While the model sometimes makes errors at predicting response position IDs (which we count as an error in our plots), for many of the synthetic tasks that are studied, typically each coupled position ID actually only depends on a small number of previous tokens (e.g., many of the position IDs just increment by 1 at each step). Please see Sections E.2.1 and E.3.1 for the description of our choices of coupled position IDs for our synthetic experiments.
**Regarding Assumption 3.2.** Yes, when $k = 1$, relativity leads to a sort of ``bag of words'' model which is invariant to permutations of the sequence of tokens. We believe the interesting cases occur when $k > 1$.
---
Rebuttal Comment 1.1:
Comment: Thank you for the author rebuttal.
The rebuttal has addressed my concerns about length generalization bound and details about PPC.
I raised my score to 4. | null | null | null | null | null | null | null | null |
AutoEval Done Right: Using Synthetic Data for Model Evaluation | Accept (poster) | Summary: - Paper addresses the problem of evaluating ML models with limited human validation data.
- Proposes Autoeval, an approach pairing limited human data with large amounts of AI synthetically labeled data to get model eval scores
- The primary contribution is the framework based on the existing PPI work
- Evaluations are done to estimate performance metrics directly (e.g. accuracy) and also relative model performance in the case of BT-models
- Results are positive compared to alternative approaches
Claims And Evidence: Well supported claims
- Autoeval can improve sample efficiency without introducing bias.
- PPI provides more accurate and reliable estimates than classical methods.
- Autoeval extends to ranking approaches as well.
Unsupported
- Coverage guarantees are not always obtained as shown in the results and depend on the number of labeled samples (even in cases with large CI width)
- This shows perhaps the claim on IID is not met between labeled and unlabelled
Methods And Evaluation Criteria: - The selection of benchmark datasets is strong and covers a wide variety of areas
- Method is well motivated as well as the evaluation criteria
Just flagging an assumption of the annotator model quality: The method assumes that the AI-generated synthetic labels are at least weakly correlated with the true human labels.
That said the correlations are pretty low. Is this a function of LLMs in general and why specifically are other LLMs better than others? i.e. where are they good and where are they bad
Theoretical Claims: - Theoretical claims are sounds and mainly defer back to the original PPI work & its guarantees
- However, Sec 2.2 does do some solid theoretical analysis
Experimental Designs Or Analyses: - The experimental designs are thorough and well-executed:
- The authors use a diverse set of domains (computer vision, protein fitness, LLM evaluation) to demonstrate broad applicability + good use of baselines
- It would be interesting though to understand where the method works well and where it fails. e.g. where is the approach poor, where is the correlation low (is it specific types of examples). This would greatly help with understanding
- Also it would be nice to have some runtime and cost information vs classical methods — to understand the trade-off of the gains
Supplementary Material: The code examples (and zipped code), the experimental details and extra experiments in the appendix are really nice.
I recommend moving figure S1 to the main paper since coverage is an important aspect of the paper
Relation To Broader Scientific Literature: In general pretty good
- It would be useful to augment the related work to position the work with respect to recent works on:
- LLM judges: For example: https://arxiv.org/abs/2403.02839, https://arxiv.org/abs/2412.05579
- Synthetic data for model evaluations. For example: https://arxiv.org/abs/2310.16524
Essential References Not Discussed: see above for references
Other Strengths And Weaknesses: Strengths:
- clear and well-written paper
- strong results empirically and good theoretical analysis
Weaknesses:
- Issues around novelty — seems like a repackaging of PPI for a different use case (i.e. application).
- Computational cost uncertain
- Needs to augment related work to position better as discussed above
- Add discussion of how this work might be extended under distribution shift in greater detail than the current passing references. Since likely in reality this would be use-case.
Other Comments Or Suggestions: - possible add a section on the distribution shift problem and how this could be handled
- add a section on how this would work for fairness, as it’s mentioned but never shown
- Deconstruct the method more to understand where it succeeds and where it fails — especially why it fails (types of situations)
Questions For Authors: See above points
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: We thank you for your thoughtful comments and positive feedback on the relevance of our work, the strength of our benchmark, and of our theoretical analyses. Below are detailed answers to your comments.
**Understanding when AutoEval > classic.**
Our approach adjusts to the quality of synthetic labels. In particular, AutoEval can rely on power tuning to identify the optimal λ used in Equation 4 or 6. This mechanism ensures that our estimates (i) have small asymptotic variance (ii) ignore synthetic labels when these are unreliable. Thus, our method is at least as good as the classical approach and typically better with informative synthetic labels.
We also cover several scenarios in our work where multiple synthetic annotation schemes could be competing. Figures 3 and 5 show that the correlation between synthetic and true labels is a good indicator of AutoEval performance and recommend using this metric to prioritize annotation schemes.
In the context of LLMs, we indeed note overall small correlations between human and LLM judge preferences, likely due to noise in human preferences and the ambiguity of many real-world prompts (multiple valid responses may exist). For instance, agreement rates of 85-90% among experts and 75-80% between experts and crowds have been reported in the past (see Chiang et al. 2024).
These small correlations also highlight the limitations of LLM judges, biased by answer length, position, and stylistic similarities (Zheng et al. 2023). Mitigating bias via careful prompting, randomization of answer order (Li et al. 2024), and stronger judges (e.g., via fine-tuning on human preferences) could improve effective sample sizes of AutoEval.
You also highlight the relevance of understanding which LLM judges produce high-quality synthetic labels and on what inputs. Future work could apply AutoEval to specialized areas for LLMs where validation data is too scarce to provide insights into underrepresented tasks, providing better insight into what constitutes good LLM judges across domains.
**Covariate shifts**
Covariate shifts are central to key applications of AutoEval. A common scenario arises when unlabeled inputs are drawn from a distribution different from the target distribution. Labeled inputs could themselves not be sampled from the distribution of interest. These effects are relevant to address fairness concerns. Applied to LLM evaluation, for instance, covariate shift toward specific prompts can lead to biased evaluations that are not representative of target use cases.
We will add a supplementary note on AutoEval estimators under covariate shifts. In the canonical case, when unlabeled and labeled inputs respectively drawn from distributions P and Q, we can apply AutoEval using traditional covariate shift adjustment methods. Key assumptions here are that P is absolutely continuous with respect to (w.r.t.) Q and that the Radon-Nikodym derivative of P w.r.t. Q is known.
**Novelty**
Our work is more than a repackaging of PPI for model evaluation. We outline specific theoretical and methodological novelties in our response to Reviewer 3tuY and refer you to that discussion for details.
**Runtime**
We compared runtimes between AutoEval and classical in the ImageNet experiment:
Table: Runtime comparison between AutoEval and the classical approach for the evaluation of Resnet101 in the ImageNet experiment ($n=1,000, N=50,000$). This experiment was run on a workstation with an Nvidia RTX 3090 GPU, 128GB RAM, and an i9-12900KF CPU.
| Method | prediction (s) | inference (ms) |
| :------ | :------------- | :------------- |
| classic | 5 | 0.3 |
| PPI++ | 237 | 8.3 |
The main bottleneck here is synthetic label generating, typically scaling linearly with the number of samples. This cost is generally acceptable given the gains in evaluation efficiency and statistical power. We will include this analysis in the revised Supplement.
**Other**
> Coverage guarantees are not always obtained [...]
Undercoverage in Figure S1b is due to insufficient Monte Carlo (MC) trials. Rerunning the experiment with $K=500$ MC trials yields:
Table: Coverage for $\alpha=0.1$ in the protein fitness experiment
| Method | n=50 | n=100 | n=200 | n=300 | n=400 | n=500 |
| :------ | :--- | :---- | :---- | :---- | :---- | :---- |
| PPI | 0.87 | 0.89 | 0.89 | 0.89 | 0.89 | 0.88 |
| PPI++ | 0.88 | 0.89 | 0.89 | 0.89 | 0.89 | 0.9 |
| classic | 0.89 | 0.89 | 0.89 | 0.89 | 0.89 | 0.9 |
The coverage is now much closer to nominal levels and validates our coverage claims.
> It would be useful to augment the related work [...] on LLM judges [...] synthetic data for model evaluations.
We thank you for the suggestion. Since LLM judges are core to our work, we will update the related work in the revision with the suggested references.
> I recommend moving figure S1 to the main paper [...]
We thank you for this comment and will move S1 to the main paper in the revised paper.
---
Rebuttal Comment 1.1:
Comment: Thank you for your detailed response. I appreciate the clarifications on runtime, coverage guarantees (but see comment below) and novelty.
I have the following points remaining to discuss:
1. It is important to still have the limitations analysis: concrete empirical study of failure modes — like where exactly AutoEval should not be used such that a reader can have an understanding to better know where the framework works and where it fails.
2. While I appreciate the theoretical discussion around covariate shift. Empirically, it would be useful to see how the framework is affected under shift & exchangeability is violated. Unless the below is the setting
3. On coverage guarantees — if exchangeability is satisfied, shouldn’t the marginal coverage guarantees be satisfied? i.e. 0.9 or greater. Hence, while the results from the table are close why are the guarantees not satisfied? Is it that exchangeability is not satisfied?
Looking forward to hearing from the authors
---
Reply to Comment 1.1.1:
Comment: Thank you for your follow-up comments. We hope our responses address your concerns, and we would welcome any further questions you may have.
## Covariate shifts and failure modes
We agree with your two first points.
Based on your suggestions, we will include a more comprehensive discussion on AutoEval's assumptions, and how these assumptions might or might not be violated in practical settings. Space permitting in the main manuscript, or otherwise in the Supplement referenced in the discussion, we plan to include the following:
> A key assumption to apply AutoEval is that unlabeled and labeled inputs are i.i.d. draws from the same distribution. This assumption typically applies when labeled inputs are randomly sampled from the unlabeled pool.
> When there are distributional shifts between the labeled and unlabeled inputs, this assumption might be violated.
> These distributional shifts typically arise when the labeled inputs are not sampled uniformly at random from the unlabeled pool, or when labeled and unlabeled data points come from different populations altogether.
> In such cases, AutoEval, in the form described in Equation 4 and 6, loses the statistical guarantees we outline in the paper, and confidence intervals may no longer be valid.
> To address this issue, we derived alternative AutoEval estimators that are robust to covariate shifts (see Supplement).
> As an illustration, we revisited the ImageNet experiment, with a new setting where the labeled and unlabeled data points are not exchangeable (Table B).
> In this setting, we found that the confidence intervals from AutoEval estimator from Equation 4 were dramatically overconfident, most likely because our experiment introduced strong covariate shifts between labeled and unlabeled inputs.
> Our reweighted AutoEval estimator, on the other hand, provided calibrated confidence intervals.
> These results demonstrate that the original formulation of AutoEval is sensitive to covariate shifts.
> A critical requirement for valid application is therefore careful verification of AutoEval's assumptions.
> When exchangeability is violated, alternative strategies, such as our reweighting approach, must be employed to maintain statistical validity.
Table B: Coverage for $\alpha=0.1$ in the Imagenet experiment under covariate shifts. To introduce covariate shifts, we sampled labeled data points weighted by the probabilty predicted by Resnet101 on one of the 1000 ImageNet classes.
| AutoEval estimator | unweighted | reweighted |
| ------------------ | ----------- | ----------- |
| n=50 | 0.5044 | 0.9128 |
| n=100 | 0.3780 | 0.9196 |
| n=200 | 0.2444 | 0.9184 |
| n=300 | 0.1992 | 0.9376 |
| n=400 | 0.1692 | 0.9252 |
| n=500 | 0.1572 | 0.9320 |
In addition to this discussion, we plan to include a detailed description of the reweighted AutoEval estimator in the Supplement, implementing the strategy proposed in our last response.
Over, we believe this discussion better highlights the importance of exchangeability to produce valid inferences, while providing practical guidance on how to proceed when exchangeability is violated.
We thank you for this suggestion, and would be happy to discuss this further.
## Coverage guarantees
Regarding your third point, we would like to clarify that in the data we showed in our last response, exchangeability was satisfied.
In addition, the fact that the empirical coverage is lower than the nominal coverage (e.g., 0.88 instead of 0.9) is not statistically significant.
To validate this claim, we rerun the coverage experiment from our last response, this time with confidence intervals on the coverage estimates (Table C).
As you can see, the 0.9 nominal coverage is contained in all cases, showing that the coverage guarantees hold empirically.
Table C: Coverage for $\alpha=0.1$ in the Imagenet experiment with 95% asymptotic confidence intervals on the coverage estimates.
| Method | n=50 | n=100 | n=200 | n=300 | n=400 | n=500 |
|---------|-------|--------|--------|--------|--------|--------|
| PPI | 0.867 $\pm$ 0.096 | 0.886 $\pm$ 0.064 | 0.893 $\pm$ 0.044 | 0.890 $\pm$ 0.036 | 0.890 $\pm$ 0.031 | 0.882 $\pm$ 0.029 |
| PPI++ | 0.881 $\pm$ 0.092 | 0.887 $\pm$ 0.063 | 0.891 $\pm$ 0.044 | 0.886 $\pm$ 0.037 | 0.889 $\pm$ 0.031 | 0.897 $\pm$ 0.027 |
| classic | 0.887 $\pm$ 0.089 | 0.887 $\pm$ 0.063 | 0.895 $\pm$ 0.043 | 0.887 $\pm$ 0.037 | 0.891 $\pm$ 0.031 | 0.898 $\pm$ 0.027 | | Summary: This paper proposes an approach called "autoevaluation". Given a small set of human-labelled examples, and a larger set of (iid) unlabelled examples, the proposed algorithm can synthetically assign labels in a comparatively efficient and unbiased manner. The authors validate their approach using experiments on real-world tasks such as ImageNet, Protein fitness prediction, and chatbot arena.
Claims And Evidence: Yes, the major claims made in this paper seem well-supported.
Methods And Evaluation Criteria: Yes the proposed PPI-based approach appears to be sound. The empirical evaluation is on standard datasets.
Theoretical Claims: Yes the calculation of confidence intervals in section 2.2 looks correct to me. However, I am not an expert in this area so it is possible I may have missed something.
Experimental Designs Or Analyses: The experiments presented are a straightforward application of the proposed approach and look sound to me.
Supplementary Material: No
Relation To Broader Scientific Literature: There is growing interest in synthetic data generation and annotation in the field of evaluation considering the fact that human annotation is expensive, and sometimes impractical.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: One issue I have with this line of work is that it makes a set of assumptions (1) existence of unlabelled inputs, and (2) the unlabelled inputs are iid. Considering the state of evaluation in ML wrt to large models, I think it has become increasingly important to curate more challenging evaluation benchmarks. In this respect, generating (or labelling) more examples which are iid to benchmarks that we already have (and have presumably been saturated by large models) doesn't really feel like a particularly impactful step forward towards solving our evaluation troubles. Even if we design a new (not-yet-saturated) benchmark with a few human-labelled examples, how valuable is it actually going to be to scale it up with AI-based labelling? Further note that one of the actual bottlenecks in creating effective benchmarks is designing the "hard inputs" (which this paper assumes we already have access to).
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your kind and insightful comments. We are grateful for your appreciation of our work, particularly our methodologically sound approach and practical demonstration of efficient model evaluation across multiple domains.
Regarding your comment on the relevance of AutoEval to address benchmark saturation, we would like to highlight a central application that motivates our work. One major inspiration for this work is the chatbot arena project (Chiang et al. 2024). This project serves as a dynamic alternative to traditional static benchmarks, allowing human participants to compare and vote on large language model (LLM) responses..
Despite the availability of large amounts of human validation data, resolving ties between models remains challenging in this project.
First, many users prompt models with questions but decide not to provide preferences between models. Consequently, a large number of conversations without human preferences is available, which cannot be leveraged by traditional model evaluation approaches.
There are also many cases where there is not enough validation data to resolve ties between LLMs. This can happen when a new LLM releases, requiring large amounts of votes (which may correspond to several days of traffic) to quantify its relative performance.
Unresolved ties also occur when evaluating model performance on specific applications where relevant conversations are limited, such as coding assistance or creative writing, for instance. Helping resolve ties timely in dynamic benchmarks such as Chatbot Arena with AutoEval is one way we believe our work can help address benchmark saturation.
We agree with your observation regarding the i.i.d. assumptions in our work. In the chatbot arena, for instance, these assumptions are challenged when users ask multiple questions or repeat the same question, leading to data dependencies. To address this, future work should extend AutoEval to more general settings with data dependencies to produce reliable inferences.
Finally, AutoEval does not solve the problem of designing hard inputs. It builds on the assumption that inputs are easy to sample but harder to label. While this assumption is limiting, the applications of our work—including in NLP—show that this paradigm can be useful. Beyond NLP, labeling at scale remains a significant challenge in many domains, such as biomedical applications, where we believe AutoEval can make an impact in facilitating model evaluation. | Summary: This paper studies an important question in auto-evaluation --- how to efficiently combine model prediction (imputed output) for abundant unlabeled data with limited gold-standard data to obtain efficient estimation for expected metrics for underlying distributions. The paper's method is a direct result from a recent line of paper in prediction-powered inference, the only difference is that they used for evaluation instead of inference. Experiments have been done for interesting applications such as pairwise comparison etc.
Claims And Evidence: Yes, the claims are clear and evidence seems good.
Methods And Evaluation Criteria: Yes, it makes sense. Mostly about directly measuring MSE and effective sample size. But this method could also provide confidence intervals based on asymptotic normality, and this paper did not include that in most of experiments, only in one in Appendix C.
Theoretical Claims: The theoretical claims are correct but largely could be directly derived from PPI++, did not have much innovation. I wouldn't claim any innovation in theory for this paper.
Experimental Designs Or Analyses: I think the experimental designs and fine but still limited. For instance, coverage did not include for most of the experiments, and whether other metrics beyond MSE could be considered is not discussed. For instance, some cross entropy type of metrics are very widely used, but not discussed as metrics here. I understand this work largely studies unbiased estimator, so if the final aim is MSE, then the only thing we need to do is to reduce variance. But I would like to see other metrics discussed.
Supplementary Material: Yes, I looked through all the parts in the supplementary material.
Relation To Broader Scientific Literature: I think it is useful in practice, but also am concerned that the results by simply using gold-standard data are already good enough, the improvement seems marginal.
Essential References Not Discussed: NA.
Other Strengths And Weaknesses: I think the problem itself is important but theoretical innovation is quite limited. Also, the experimental results are not comprehensive enough (see above comments).
Other Comments Or Suggestions: Please see above.
Questions For Authors: NA.
Code Of Conduct: Affirmed.
Overall Recommendation: 1 | Rebuttal 1:
Rebuttal: We thank you for your detailed and thorough feedback. We are grateful for your acknowledgement of the importance of the problem we are tackling, on the clarity of our claims and the methodological soundness of our approach.
Your review raises a number of points relating to the theoretical contributions and to the experimental design of our work. Please find below our detailed response to these points, that we hope will address your concerns.
**Lack of theoretical contributions.**
We would like to address your concerns about the theoretical contributions of our work. While our approach indeed builds upon the prediction-powered inference (PPI) framework, it contains several novel theoretical and modeling aspects, relevant both in the context of auto-evaluation and PPI.
The first contribution is to build a general framework for model evaluation using synthetic labels.
For metric-based evaluation, our framework accommodates various and nontrivial synthetic annotation schemes (e.g., external model annotation, or self-annotation, see Section 2.1), and allows both for hard or soft synthetic annotations. We also extend this framework to comparison-based evaluation, enabling rigorous model performance inference from pairwise comparisons.
Our work also introduces chi-squared confidence sets for PPI, an important extension of the original PPI machinery that is not covered in the original papers. Indeed, PPI and its extensions typically focus on simple, low-dimensional inference tasks. The realization that chi-squared confidence sets can be used may open up new research directions to extend the PPI framework to higher-dimensional problems.
These developments, along with the demonstration of the practical applicability of our framework across a variety of tasks and domains, highlight that our work is more than a direct result of the PPI framework.
More importantly, we believe our work is particularly timely and of significant scientific relevance given the growing need for efficient evaluation of increasingly complex machine learning models across scientific disciplines. This need is particularly obvious in the context of LLMs, where even crowdsourced validation like Chatbot Arena (Chiang et al. 2024), studied in our work, often suffers from insufficient data to resolve ties between models.
**Marginal improvements relative to the classical approach**
The other concern we would like to address relates to the perceived magnitude of improvement over the classical approach. In our experiments, AutoEval reaches efficiency ratios (effective sample sizes over sample sizes) between 1.25-1.40. Another way to appreciate these numbers is to think about the width of the obtained confidence intervals. An efficiency ratio of 1.25 translates into a 11% reduction in the width of confidence intervals, which, as shown in our experiments, significantly facilitates model ranking. See for instance Fig. 1c, where tighter confidence intervals translate for most sample sizes into at least a two-fold improvement in predicted rank correlation with ground-truth.
We believe these numbers are meaningful and highlight the practical relevance of our work in a variety of ML settings. That being said, the practical relevance of this improvement depends on the financial and time costs to produce human and synthetic validation data. Our method is particularly relevant in instances where human validation cannot be obtained in a timely manner. Examples include the Chatbot arena, where human annotation depends on web traffic, which cannot be controlled, or in biological assays where obtaining validation data may take weeks or months, but where producing large amounts of synthetic data can be done in a few hours.
**Benchmark**
> But this method could also provide confidence intervals based on asymptotic normality, and this paper did not include that in most of experiments [...].
We would like to make an important clarification, as building valid confidence intervals of model performance is central to our work. In particular, Figure S1 of Appendix C shows confidence intervals not for one, but all of the main experiments (in Sections 2.3, 2.4, and 3.3) considered in this work.
These confidence intervals, which we demonstrate are well-calibrated and tighter than classical approaches in all experiments, are fundamental to our methodology as they enable statistically rigorous model comparison and selection even with limited labeled data.
> I would like to see other metrics discussed.
We thank you for suggesting the exploration of additional metrics. In response, we have extended our analysis in the following way. We studied confidence interval coverage for multiple alpha values (0.8, 0.85, 0.9, and 0.95) beyond the original α=0.1, confirming consistent calibration across confidence levels.
Regarding cross-entropy metrics, we would appreciate your clarification on how you envision these metrics being applied in our evaluation framework.
---
Rebuttal Comment 1.1:
Comment: Thanks for the response.
1. I think the claimed contribution in theory is not actually considered theoretical contribution, I would rather consider it is just different specific application scenarios. The key core theoretical tool is just PPI++, with an even simpler form, it will not need to go into Taylor expansion for M-estimation etc. It is just a simple application of CLT for i.i.d random variable.
2. I take a look at Appendix C, I don't know whether it is the demonstration problem at my end, I did not see the results of intervals. Actually, Figure a and c in Appendix C are not showing up at all!
I will remain my score.
---
Reply to Comment 1.1.1:
Comment: Thank you for your follow-up. Regarding point 1, we respect your assessment of our theoretical contributions while maintaining our view,
outlined in our previous response, that the work offers meaningful extensions to the PPI framework in the context of evaluation.
For point 2, we apologize for the technical issue you experienced with Figure S1 in Appendix C.
We confirm, after manual inspection, that Figures S1a and S1b are included in our submission: https://openreview.net/pdf?id=S8kbmk12Oo
On our end, these figures are properly displayed on OpenReview using a Chrome or Firefox browser and on Adobe Acrobat Reader after manual download.
To reproduce your issue, however, we did observe that figures S1a and S1c are not properly displayed on Safari.
We will make sure to understand this issue and fix it in future versions of the manuscript.
Meanwhile, we invite you to download the pdf or use another browser in case you are using Safari. | Summary: The goal of this work is to reduce the cost and time of evaluating machine learning models using AI-labeled synthetic data. Introduces algorithms for auto evaluation that improve sample efficiency while remaining unbiased.
Claims And Evidence: • This problem has been tackled in the literature with different names: pseudo-labeling, curriculum learning, consistency regularization etc. It is important to compare the proposed method against previously published work.
• Evaluation of LLM responses from pair-wise responses has also been studied in measuring uncertainty using structural similarity and other pair-wise metrics.
• The proposed problem statement is relevant for training samples as well.
• The effective sample sizes considered are very small, and important to evaluate the approach with larger datasets.
• The claim that proposed methodology provides calibrated and tight confidence intervals is clearly apparent (presented in supplemental material). Need to compare with other principled uncertainty metrics.
Methods And Evaluation Criteria: The approach is evaluated on Imagenet, protein fitness experiment and pairwise preferences for LLMs. The evaluation is limited.
Theoretical Claims: There is no clear theoretical justification for PPI++ metric.
Experimental Designs Or Analyses: see above sections.
Supplementary Material: -
Relation To Broader Scientific Literature: -
Essential References Not Discussed: -
Other Strengths And Weaknesses: -
Other Comments Or Suggestions: -
Questions For Authors: -
Code Of Conduct: Affirmed.
Overall Recommendation: 2 | Rebuttal 1:
Rebuttal: We thank you for your comments. We appreciate your recognition of our work's practical relevance in reducing ML evaluation costs and the strength of our benchmark.
Please find below point-by-point answers to your comments.
**Positioning of our approach relative to semi-supervised training strategies.**
> This problem has been tackled in the literature with different names[...]. It is important to compare [...] against previously published work.
Thank you for the comment. Although these previously published topics handle related topics, our work is very different and does not fit in these existing areas. The fundamental reason is simple: our work is about evaluation, and your suggested topics are about model training.
To elaborate, pseudo-labeling uses predicted labels for unlabeled data as ground-truth during training (Lee 2013; Arazo et al. 2020). Curriculum learning is another model training paradigm that progressively increases training difficulty, e.g., via multi-stage training, to improve generalization (Bengio et al. 2009). Consistency regularization aims to enforce semantically similar inputs to have similar label predictions, relevant in semi-supervised training settings (Bachman, Alsharif, and Precup 2014; Laine and Aila 2016).
The key difference is that our focus is on the reliable evaluation of already trained models, rather than the training of these models on limited data. Our framework provides strong guarantees on the behavior of model performance estimates which is not the case for the mentioned literature. While these guarantees may not be relevant in a model training setting, they become crucial when evaluating models before deployment.
> The proposed problem statement is relevant for training samples as well.
While PPI can be employed for training purposes, this direction is beyond our scope, and we make no claims for training applications. We plan to revise our related work to cover synthetic label for model training to emphasize distinctions with our work.
> Evaluation of LLM responses [...] has also been studied in measuring uncertainty using structural similarity and other pair-wise metrics.
Thank you for pointing towards this related research area. A growing body of literature has indeed focused on evaluating LLMs from pairwise comparisons, often using LLMs as judges. We will revise the manuscript to include a more comprehensive and detailed discussion of this literature by including the references mentioned by Reviewer f29Q.
**Benchmark**
> The effective sample sizes considered are very small, and important to evaluate the approach with larger datasets.
The labeled sample sizes in our work are small to illustrate practical settings with limited human validation; however, the results certainly hold for larger sample sizes. To address this point head-on, we studied the behavior of AutoEval for larger sample sizes in the imagenet experiment, as shown below:
Table: ImageNet experiment for $n=10,000$.
| Method | MSE (1e-5) | Interval width | Coverage ($\alpha = 0.1$) | Efficiency ratio ($ESS / n$) |
|---------|-----------|----------------|-----------|-----------------|
| classic | 1.43 | 1.37 | 0.93 | 1.00 |
| PPI | 1.07 | 1.21 | 0.931 | 1.27 |
| PPI++ | 1.03 | 1.19 | 0.93 | 1.29 |
Above, AutoEval compares favorably to the classical approach for pointwise performance evaluation. It also provides tighter confidence intervals, large effective sample sizes, and proper coverage.
> The claim that proposed methodology provides calibrated and tight confidence intervals is clearly apparent [...]. Need to compare with other principled uncertainty metrics.
To answer your comment, we conducted additional analyses to evaluate confidence interval calibration across significance levels (0.8, 0.85, 0.9, and 0.95), and compared directly with the classical approach. The results, to be included in the revised Supplement, demonstrate our confidence intervals maintain proper calibration across these significance levels.
Empirical coverage closely matches the nominal coverage, indicating well-calibrated uncertainty estimates for AutoEval. We hope this addresses your concern, and would be happy to implement other metrics if you have other suggestions.
> The approach is evaluated on Imagenet, protein fitness experiment and pairwise preferences for LLMs. The evaluation is limited.
The current manuscript describes several canonical applications of our framework, for a variety of tasks, in model evaluation and ranking across different domains. We believe that the current benchmark offers a comprehensive evaluation of the proposed framework in a variety of real-world settings.
**Other comments**
> “There is no clear theoretical justification for PPI++ metric.
We would be happy to take your suggestions into account to clarify the distinctions between PPI and PPI++ if our description lacked clarity. Could you expand on which specific section of the paper you are referring to? | null | null | null | null | null | null |
Regression Trees Know Calculus | Reject | Summary: The paper proposes a method to obtain gradients from regression trees. The gradient estimate is similar to a finite difference using mean responses across splits divided by size of node along dimension. Paper presents a Monte Carlo estimator and a partition-based estimator of integrated gradient quantities. Paper presents convergence of the gradient and integrated gradient estimators. Experiments include visualization of integrated gradient for MNIST digit classification, prediction error on rotated feature matrices, active subspace error compared with other methods, and dimension reduction using active subspace.
Claims And Evidence: claim is that paper developed a gradient estimator (and integrated gradient estimator) for regression trees. This claim has qualitative evidence from Fig. 1. The proofs provide theory that estimators converge to true values.
Claim is that gradient of regression trees is useful/performs better than other methods for integrated gradients and active subspace. The tree-based active subspace (TBAS) rotation augmented regression had lower or equal error compared with other methods. The TBAS had lower error or execution time compared with other methods (fig 5, 6). TBAS can be used for dimension reduction / interpretability (fig 7, 4).
Methods And Evaluation Criteria: Integrated gradient for trees included qualitative evaluation of MNIST digits.
In the active-subspace rotation experiment, paper compares the RMSE of regression tree or random forest trained on augmented rotation data by TBAS, PCA, and random orthogonal directions. This seems reasonable.
Paper claims that tree-based active subspace estimation is faster and lower error than other methods (DASM, GP, PRA). Evaluation is a comparison of error and execution time. This part would benefit from complexity analysis if available.
Dimension reduction using TBAS was evaluated qualitatively, with the first most important variable matching one other study.
Theoretical Claims: Did not look into in detail. Seems reasonable since estimators match intuition for finite difference.
Experimental Designs Or Analyses: see methods/evaluation section.
The experiments presented do not include a quantitative verification of the asymptotic correctness of gradient / integrated gradient estimate. Paper states a limitation is very deep regression tree may be required for high-dimensional dense gradient. Paper is missing the experimental analysis of depth of gradient required, and the effect of relevant factors (total data, number of dimension, density of gradient etc).
Supplementary Material: Supplemental has code. Appendices have proofs, experiment details, and additional figures. Fig. 8 and 9 are same figure.
Relation To Broader Scientific Literature: Paper points to Chaudhuri 1995 and Low 2011 as papers looking at gradients for tree based models. Paper fits in with literature on integrated gradient and active subspace method.
Essential References Not Discussed: not familiar enough with area to know
Other Strengths And Weaknesses: Strengths: The concept of the paper (gradients for tree models) seems original. There is a good amount of comparison with existing methods in the experiments section.
Weaknesses: Claims of computational efficiency are less convincing. Paper could be improved by including theoretical complexity across methods, including proposed method. Paper states a limitation is very deep regression tree may be required for high-dimensional dense gradient. Would be good to see quantitative and empirical analysis of this.
Other Comments Or Suggestions: line 270 "we begin with MCE", then following line is about PBE.
line 273 typo.
line 368 typo.
line 348 typo.
typo in Fig 7 caption.
Fig 8 and 9 are same figure.
Questions For Authors: 1. What is the color representing in Fig. 7? What is the takeaway from Fig.7 right panel?
2. What is the x axis representing in Fig. 6?
3. On Fig. 4, why is IG only shown on the dark pixels of digits? Is the IG value low for everything not shown?
4. Would be good to know how parameters affect the tree based gradient estimates in the empirical setting.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks much for your helpful comments. In addition to our responses to your helpful feedback and questions, we have conducted a new simulation study investigating the empirical performance of our method in estimating gradients (see below and Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)).
**Regarding: "Claims of computational efficiency are less convincing. Paper could be improved by including theoretical complexity across methods, including proposed method."**
Great idea: mathematical complexity is a great starting point; we comment on it below and will add this discussion to the paper. However, it is somewhat limiting in this context with competitors defined via nonlinear optimization, as efficiency depends on how many training iterations are necessary. While we can compute the per-iteration complexity, this may not be reflective of the actual performance. This is what motivated us to use Wall time to measure computational efficiency in Figure 5 of the original article, which showed that, empirically, the tree-based methods are considerably more 1-2 orders of magnitude more efficient than the comparators.
We now give theoretical complexity estimates for each method. We have added this discussion to the article.
i) Regression Tree: Fitting a tree is of complexity $PN\log N$ (e.g. Chen and Guestrin 2015's xgboost paper). Then, computing the gradient estimates requires a fixed number of computations at each decision node in the tree, of which there are on the order of $N\log N$. Storage is $P N\log N$ as each node has a gradient estimate.
ii) Gaussian process: Evaluating the likelihood is of complexity $N^3P$. The number of iterations required is dependent on the exact sampling scheme and function, and not well understood. After fitting the model, the active subspace can be extracted with complexity $N^2P^2$.
iii) Polynomial Ridge Approximant: This is solved via a nonlinear least squares problem, and each iteration will have complexity $NPR$ where $R$ is the active subspace dimension. Like GPs, the number of iterations needed to converge is difficult to do analysis on. However, once the analysis is done, the active subspace matrix is immediately available with no further computations.
iv) Deep Active Subspace. This involves fitting a neural network. The per-iteration complexity scales with $MP$, where $M$ is the minibatch size and $P$ is the input dimension, and this value is scaled by the time it takes to do a forward pass through the network. Like the GP and PRA, the exact number of iterations required is difficult to know. Also like the PRA, the first weight matrix encodes the active subspace.
**Paper states a limitation is very deep regression tree may be required for high-dimensional dense gradient. Would be good to see quantitative and empirical analysis of this.**
Thanks for suggesting that we look further into this. We have conducted a new simulation study investigating the impact of tree depth on Gradient performance on the function $f(x) = \log(1+a^\top x/P)$ with nonzero elements of a generated from an iid Gaussian, which shows the convergence in finite samples explicitly. See Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe) for results. The left column shows the performance when the Depth=4, and the right column for Depth=12. The x axis in each pane gives sample size and the y axis gives dimension. We see that when Depth=4, there is essentially no reduction in error. By contrast, when Depth=12, the error decreases to zero with larger sample size, illustrating the importance of depth. We have added this experiment to Section 5.
**Figure 8 and 9 are same figure.**
Thanks so much for pointing this out; Figure 9 was supposed to give the boxplots for classification, but we accidentally replicated the regression results because the filenames were similar. We have fixed this.
**"What is the color representing in Fig. 7? What is the takeaway from Fig.7 right panel?"**
Thanks for pointing out that we did not mention that the color indicates the predicted value; pink is low and blue is high. The take-away from the right panel is that the predictive surface is actually quite simple when viewed via the active subspace, and is almost like an "XOR" shape.
**"What is the x axis representing in Fig. 6?"**
x-axis is sample size; y-axis is angle between true and estimated subspace.
**On Fig. 4, why is IG only shown on the dark pixels of digits? Is the IG value low for everything not shown?**
Since the reference image is all white, any white pixel in a target image will have IG 0.
**Would be good to know how parameters affect the tree based gradient estimates in the empirical setting.**
See discussion of the additional new Figure 1 above.
Thanks for your suggestions that we look into the computational efficiency and depth requirements; we think addressing these concerns has much improved the article. | Summary: The paper develops a simple and computationally efficient approach for estimating gradients from a decision tree, essentially by computing a finite difference across all of the nodes on the way to the leaf that contains the point at which a gradient is required. These gradients are then used for active subspace estimation and computing integrated gradients.
## update after rebuttal
Score up to Accept
Claims And Evidence: The paper provides a thorough theoretical analysis to support what on the surface seems a fairly natural and straightforward approach to estimating gradients from a decision tree. Overall I felt like the claims made by the paper are well-supported, with some qualifications below.
Methods And Evaluation Criteria: The use of active subspace as a way of evaluating the approach is great, and shows a real use-case. Derivative-based sensitivity analysis is another one that the authors could consider for the future, and where there are standardized benchmark problems and existing (GP-based usually) baselines.
Theoretical Claims: Not in detail.
Experimental Designs Or Analyses: I was confused by the use of random forests in 5.1. It seems that the gradients are themselves being computed on the random forest model? Is that as the average of the gradients across the forest or something? Or is a separate regression tree being used as an explanation model?
Generally, the empirical evaluation covers two things: integrated gradients for model explanation, and active subspace estimation for rotation or dimensionality reduction. I didn't see any issues with the experimental design related to active subspace estimation. For integrated gradients, the evaluation is much weaker, and in fact is not really an evaluation but rather an illustration, lacking comparison methods or ground truth. (The paper describes it as a "qualitative study," which is somewhat euphemistic).
There is a third empirical evaluation that I think would be important for a paper like this but doesn't seem to be present: evaluation of the actual quality of the derivative estimates. A major claim of the paper is that regression trees can be used for uncertainty quantification, displacing models like GPs that are usually used for estimating gradients of black-box functions. But all of the evaluation is on downstream uses of gradients. How about an evaluation just of how the gradients compare to ground truth, compared to a GP estimate of the gradients? There is a large number of smooth benchmark problems used for global sensitivity analysis that would be suitable for this type of experiment. This is a pretty major hole in the paper I think, as I don't feel confident that the method is necessarily computing gradients as well as a GP on low- or mid-dimensional problems with dense gradients (a distinct task from active subspace estimation, but vital for many UQ problems).
Supplementary Material: Yes, experiment extra details and the code.
Relation To Broader Scientific Literature: The relation to broader scientific literature seems OK to me.
Essential References Not Discussed: Not that I'm aware of.
Other Strengths And Weaknesses: Overall the paper is very well-written and presents what may be a useful method.
Is it true that decision trees are a workhorse of the contemporary data scientist? I see this as true via their use as a component in Random Forests and XGBoost, which I would certainly agree are workhorses of the contemporary data scientist. The paper would be strengthened by some analysis of how the method can be used together with Random Forests in particular. The obvious thing would be average gradients across the forest, but the paper describes deep trees as being important for estimating gradients, while Random Forests are usually ensembles of shallow trees. The authors thoughts on this question would be very helpful.
Other Comments Or Suggestions: typo at the bottom of page 4, "nod x"
bottom of page 5, "fit the to two subsets"
Questions For Authors: * Can you provide evaluation of how accurately the derivatives are estimated in low- to mid-dimensional problems with dense gradients, compared to a GP and ground truth?
* Can this method be used together with a random forest?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks much for your helpful comments. In addition to our responses to your feedback and questions, we have conducted two new simulation studies, 1) investigating the empirical performance of our method relative to Gaussian Processes in estimating gradients (see below and Figure 2 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)), and 2) investigating the empirical accuracy of our method (see below and Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe))
**Regarding: “I was confused by the use of random forests in 5.1. It seems that the gradients are themselves being computed on the random forest model? Is that as the average of the gradients across the forest or something? Or is a separate regression tree being used as an explanation model?”**
Thanks for pointing out that this was not well-explained; we indeed used an average of estimates from each tree within the forest as our estimator for the whole forest. We have added a discussion of this to Section 5.2.
**Regarding: "There is a third empirical evaluation that I think would be important for a paper like this but doesn't seem to be present: evaluation of the actual quality of the derivative estimates. A major claim of the paper is that regression trees can be used for uncertainty quantification, displacing models like GPs that are usually used for estimating gradients of black-box functions. But all of the evaluation is on downstream uses of gradients. How about an evaluation just of how the gradients compare to ground truth, compared to a GP estimate of the gradients? There is a large number of smooth benchmark problems used for global sensitivity analysis that would be suitable for this type of experiment. This is a pretty major hole in the paper I think, as I don't feel confident that the method is necessarily computing gradients as well as a GP on low- or mid-dimensional problems with dense gradients (a distinct task from active subspace estimation, but vital for many UQ problems)."**
Thanks for this comment; we agree that it’s helpful to have a direct evaluation of the gradient estimate quality. We have implemented a new simulation showing the empirical performance of TBGE in estimating gradients under various tree depth, sample sizes, dimensions and gradient densities on the function $f(x) = \log(1+a^\top x/P)$ with nonzero elements of a generated from an iid Gaussian, which shows the convergence in finite samples explicitly. See Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe) for results. We have added this experiment to Section 5.
Regarding the comparison to GPs: we certainly don’t think that tree-based methods will displace GPs for gradient estimation on all problems. In small dimension with smooth functions, a dense gradient and a small sample size, a GP will greatly outperform the TBGE. In fact, for a sufficiently smooth function, we suspect a GP will basically always outperform a TBGE for a fixed sample size. However, the relative scalability of regression trees compared to GPs means they may be more attractive in large sample settings, even for dense estimators in lower dimension, particularly under noise and when speed is more important than efficiency. To illustrate what we mean, we consider the problem where the simulator of interest is relatively cheap to evaluate, and we have a large number of samples which we wish to use to estimate the gradient in several locations in the input space. We have conducted three simulation studies estimating gradients on the Levy, Cosine Ridge function, and Ackley function with variable sample size and iid Gaussian noise with standard deviation 0.1 (results in Figure 2 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)). The x-axis shows not sample size, but the elapsed real time. We see that using a regression tree on a larger dataset can give a better time-accuracy trade-off for lower accuracies than a GP on a smaller dataset. Additionally, on the Ackley function, the function is sufficiently rough that the GP often treats that variability as noise, and is unable to effectively form gradient estimates, whereas the regression tree is able to.
Certainly, we don’t mean to suggest that analysts can throw away all their existing methods for gradient estimation; but on problems in moderate dimension or with low effective dimension and many datapoints, we found TBGE to perform well, and we think this is a really interesting finding given how small a roll regression trees play in the UQ space today.
Thanks very much for challenging us to consider these new aspects of our method; we think that addressing them has improved and clarified the article.
---
Rebuttal Comment 1.1:
Comment: Thank you for the new results and additional analysis. I think the paper is strengthened by including some more detail on the situations in which this approach should be used vs. GP. In any case, there certainly are situations in which this will be a useful tool. | Summary: The paper proposes an estimator of gradients and integrated gradients based on regression trees. The proposed method estimates function gradients by finite differences between adjacent regions split by a regression tree node. Building upon this estimator, Monte Carlo based and partition-based estimators are developed to estimate integrated gradients. Theoretical guarantees of the estimation consistency are also developed in the paper. The proposed method is then applied to active subspace methods for dimension reduction and integrated gradient methods for model interpretation.
## update after rebuttal
I thank the author(s) for their detailed rebuttal and additional experiment results. Most of my concerns are resolved and I am raising my score to 4.
Claims And Evidence: The claims in the paper are in general grounded. With that being said, the paper misses some important aspects in methodology and experiments, making the results not entirely convincing. Please see my comments in the "Methods And Evaluation Criteria" section and the "Experimental Designs Or Analyses" section.
Methods And Evaluation Criteria: Overall, the proposed methodology in the paper is technically sound. Some clarification on the following questions would be appreciated:
* My understanding is that the estimators rely on a sufficiently deep regression tree. In practice, how should one tune the depth of the tree when using, e.g., TBAS?
* Instead of using a single deep tree, would a tree ensemble help with the estimation?
* The gradient estimators rely on the splits on each covariate, but this could be in trouble when the covariates are highly correlated, since the tree may always split on one covariate but never split on the other. How would the proposed method handle such scenarios?
Theoretical Claims: The theoretical results in the paper are stated in a rigorous manner, except for Theorem A.1, where it is unclear whether the result is almost sure convergence or convergence in probability.
I briefly reviewed the proofs and they look reasonable to me, though I did not carefully examine them line by line.
Experimental Designs Or Analyses: The experiments are well-designed to cover different use cases. However, some aspects are not assessed or discussed in the experiments:
* While Theorem 4.1 establishes the large sample property of the proposed gradient estimator, what would be its empirical performance with finite sample size?
* Related to my previous comment on correlated covariates, how would this affect the performance of gradient estimation and active subspace discovery?
* The simulation experiments in Sections 5.3 and 5.4 only consider noiseless observations. It would be interesting to see how the active subspace estimation performance under different noise levels.
* It would be interesting to compare the empirical performance of Monte Carlo based and partition-based integral estimation.
* In the experiments, what regression tree hyperparameters did you use to fit TBAS?
Supplementary Material: I carefully reviewed the appendices related to experiments, and briefly reviewed the technical details in Appendix A.
Relation To Broader Scientific Literature: The paper presents an interesting and novel decision tree based methods for estimating gradients and integrated gradients, which provides a promising alternative to existing active subspace estimation methods in my opinion.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Please see my comments in "Relation To Broader Scientific Literature" for the assessment of the paper's novelty and contribution.
Other Comments Or Suggestions: The paper is well-written, except for some minor issues:
* The notations for $u$ and $l$ in Algorithm 1 are different from the ones used in Equation (3).
* Line 207, LHS: "We begin with the MCE" should be "We begin with the PB".
* The Appendix needs careful proofreading. For instance,
* Line 552: Is Theorem A actually Theorem 4.1?
* Line 612: Is Proposition 1 actually Theorem 4.1?
* Lines 605 and 644: "Under Assumptions A and A"
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thanks much for your helpful comments! In addition to our responses to your feedback and questions, we have conducted three new simulation studies 1) investigating the effect of correlation on our gradient estimates (see below and Figure 6 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)), 2) investigating the empirical performance of our method in estimating gradients (see below and Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)), and 3) Investigating the impact of noise on the active subspace estimation capability (see below and Figure 3 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)).
Forgive us for being terse in some parts of this rebuttal; we ran up against the character space constraints.
**In practice, how should one tune the depth of the tree when using, e.g., TBAS?**
This is an interesting question. Our theoretical analysis suggests that the number of observations per leaf node should scale with P Log(N), and this seems to be a good default. However, it would be interesting to investigate whether it is sufficient to just tune the regression tree for predictive purposes; recent work [1](https://arxiv.org/abs/2208.10664) has found this to be the case in spline-based gradient estimation, and it’s possible that this is the case for trees as well. We think this deserves an article of its own to investigate fully.
**Regarding Tree Ensembles**
We realize the article is not clear as it stands: we do in fact perform numerical experiments which average active subspace estimates from different regression trees within a random forest. We do this via simple averaging of the estimated active subspaces, which as an average of consistent estimators will also be consistent. We have clarified this in the text.
**Regarding the effect of Correlation**
We conducted a new simulation study to investigate this interesting point (see Figure 6 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe)). Sampling data from a truncated normal in 5D with correlation varying from 0 to 0.99, we evaluated estimates of the Ackley function's gradient at 100 random points. We can confirm the effect that you have conjectured exists; intriguingly, however, it requires a very high level of correlation before the estimates are significantly affected.
**"The theoretical results in the paper are stated in a rigorous manner, except for Theorem A.1, where it is unclear whether the result is almost sure convergence or convergence in probability"**
Thanks very much for pointing out that we did not specify the convergence mode; we have clarified that we meant convergence in probability.
**Regarding empirical performance with finite sample size**
Thanks for this question; we have implemented a new simulation showing the empirical performance of TBGE in estimating gradients under various tree depth, sample sizes, dimensions and gradient densities on the function $f(x) = \log(1+a^\top x/P)$ with nonzero elements of $a$ generated from an iid Gaussian, which shows the convergence in finite samples explicitly. See Figure 1 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe) for results.
**Regarding effect of noise in active subspace estimation**
Thanks for this suggestion; we have reran the experiments in Figure 5 of the article/Section 5.3 with iid normal noise with a standard deviation of 0.1. The results are in Figure 3 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe). The comparative performances are quite similar, though the TBAS even better in dimensions 4 and 5.
**"It would be interesting to compare the empirical performance of Monte Carlo based and partition-based integral estimation".**
Thanks for this suggestion; it is always interesting to consider additional experiments, but in this case, since the Monte Carlo method converges to the partition-based method in the limit of increasing Monte Carlo sample size, we suspect that the partition-based approach would be superior.
**"In the experiments, what regression tree hyperparameters did you use to fit TBAS?"**
Thanks for pointing out that this information was missing from our appendix; we mostly used scikit-learn defaults and have added the following to Appendix B:
“””
We used the DecisionTreeRegressor and RandomForestRegressor models from scikit-learn using default parameters together with a tree depth of 4 or 8 and a minimum number of observations per node of 5.
“””
**Regarding Other Comments Or Suggestions:**
Thanks for catching the errors regarding l and u, for the “we begin with MCE” mistake, and for pointing out the labeling issue in the Appendix; we have resolved all of these issues.
Thanks very much for your thoughtful comments; you brought to light some interesting issues we hadn’t considered and we think the paper is more comprehensive now that it discusses them. | Summary: In this paper, the authors propose an efficient method to estimate the gradients of the underlying function learned by regression trees. In a nutshell, by computing a quantity resembling finite differences at a tree’s nodes—based on the extent of a given node and the function values in its subtrees—one can estimate different entries of the gradient. This allows for efficient gradient computation by simply traversing the tree and computing these values for each node. To evaluate the quality of the proposed gradient estimation method, the authors apply it in the context of model interpretability and performance improvements, specifically through Integrated Gradients, Active Subspace Estimation, and dimensionality reduction. The method outperforms existing approaches in terms of both computational complexity and predictive performance.
Claims And Evidence: One of the major claims of the paper is that the gradient estimation obtained through the proposed procedure is accurate. The authors support this claim with both theoretical analysis and experimental validation, which adequately substantiate their argument.
Methods And Evaluation Criteria: The authors validate their method on several popular tabular datasets (UCI datasets) and an image dataset (MNIST), providing insights into the effectiveness of the approach from different perspectives. However, the considered datasets are relatively small in scale (thousands of samples). Demonstrating results on larger datasets, such as (1) Criteo Conversion Log Dataset, (2) NYC Taxi Trip Duration, or (3) Higgs Boson Challenge, would significantly strengthen the paper. While it is understandable that tree-based models have their limitations, the current experiments may not be sufficient to draw confident conclusions about the method’s scalability and generalization.
Theoretical Claims: The main theoretical contributions of the paper are Theorems 4.1 and 4.2, which establish that the estimated gradient-based quantities (the gradient itself and integro-differential quantities) are close to their true values. The proposed proofs appear to be correct and valid, with no observable issues.
Experimental Designs Or Analyses: The experiments primarily use small-scale datasets, limiting the method’s generalizability. Evaluating it on larger datasets, such as (1) Criteo, (2) NYC Taxi, and (3) Higgs Boson, would better assess its scalability and robustness, strengthening the paper’s claims.
Supplementary Material: The full proofs of the main theorems and additional experimental details are provided in the supplementary material, serving as a valuable extension of the results presented in the main body.
Relation To Broader Scientific Literature: The paper clearly positions itself within the existing literature by thoroughly discussing prior work. It provides sufficient detail on potential applications of estimated gradients, such as gradient-based model interpretation, while highlighting the limitations of existing methods. More broadly, the authors present their approach as the first effective and efficient method for gradient estimation in tree-based models.
Essential References Not Discussed: No, there are no critical references missing in the paper.
Other Strengths And Weaknesses: Strengths:
* The method is highly efficient and demonstrates strong gradient estimation quality across several interesting applications.
Weaknesses:
* The generalizability of the current experimental results is a limitation. Extending the evaluation to larger datasets could significantly strengthen the contribution.
Other Comments Or Suggestions: * Figure 4: not very clear, would be good to visually highlight each pair
* Figure 7: twice "Left"
Questions For Authors: * How is the gradient computed when multiple nodes in a tree use the same feature for splitting? Is any weighting applied?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thanks much for your helpful comments! We have incorporated more datasets as suggested. Below, we discuss these new results and subsequently respond to your other helpful feedback.
**Regarding your suggestions for more datasets:**
Thanks for suggesting these datasets. We have incorporated the Taxi Trip Duration and Higgs Boson datasets into our experiments (see below), and we think they are both very interesting. However, regarding the Criteo dataset, perhaps it is simply because we are not familiar with this dataset, but it seems like the predictor variables are primarily categorical. As such, we are not usefully able to define derivatives for them and we did not include this dataset.
The Higgs Boson dataset seems perfect to demonstrate the advantage of our method, with a moderate dimension and huge dataset size. Indeed, our TBAS significantly outperforms the other transformations on this dataset; and did not misclassify a single observation in our experiments, leading to a 0% error rate (the other methods are around 1%; see Figure 4 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe); RMSE on a classification problem gives Brier Score). The taxi dataset is somewhat less within the optimal target application, having just a few variables, namely latitude, longitude and time for pickup and delivery, together with number of passengers. Feature engineering is presumably key to making good progress on this problem, and we are not time-series experts. Nevertheless, the TBAS still outperforms the identity and random transformation. However, the PCA-based method totally outperforms all other approaches on this dataset! We were very surprised by this given how low dimensional the problem was (i.e. we didn’t expect any transform to have much of an effect) and don’t yet have an explanation for this phenomenon. See again Figure 4 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe). We will fold these results into Tables 1 and Figures 8 and 9 of the article.
**Question: How is the gradient computed when multiple nodes in a tree use the same feature for splitting? Is any weighting applied?**
In this article, we simply “overwrote” the previous estimate of the partial derivative from the node earlier in the tree with the later node. We think that using some kind of weighted combination between the two could indeed yield better performance, but significant though would have to go into this to determine what the optimal trade-off is between using the coarser estimate with more data (but which is less localized) and the finer, localized estimate with less data. This would depend probably on something like the local Lipschitz constant of the function, and we think there is significant analysis and computational experiments needed to determine the best way to do this.
**Regarding the “Other comments”:**
Thanks for very much for pointing out the error in Figure 7 (it’s been corrected); thanks for pointing out that Fig 4 was unclear; we have added lines between each pair to make it clearer, see Figure 5 [HERE](https://imgur.com/a/icml-11817-rebuttal-yyVmZpe).
We think the paper is already much improved by your suggestions and especially with the inclusion of these new datasets; thanks again for your helpful review. | null | null | null | null | null | null |
TopoTune: A Framework for Generalized Combinatorial Complex Neural Networks | Accept (poster) | Summary: The paper suggests a general way to lift GNN architectures to work with simplicial and cell complexes. They implemented their project within a well-known benchmarking suite. The projected is completed with a benchmarking effort covering training on multiple classical graph datasets.
Claims And Evidence: The empirical power of the method is only somewhat supported - the experiments are run on extremely small and outdated datasets and it might be a good idea to mention that pure GNNs do a lot better on those. (For example a simple GIN from 2018 achieves more or less identical performance on MUTAG and newer methods are not even tested on them any more). This may be a problem of the field of topological deep learning that modern benchmarks are lacking.
Further claims (general method etc) are well-supported.
Methods And Evaluation Criteria: I would like to argue that the datasets are heavily outdated and should no longer be used for any scientific claims.
Also the base models are a bit simplistic, GATv2 (or better transformerconv) as message passing, as well as architectures such as GatedGCN or PNA typically work better than the basic ones used in the experiments here.
Theoretical Claims: The theoretical claims look ok, but I have not checked the proofs in the appendix. It would have been nice to mention the main proof idea in one sentence in the main paper, indicating whether the proof is straightforward and what the property hinges on.
Experimental Designs Or Analyses: I did not verify the experiments myself as the code is not yet available.
The authors state that they did only use default configurations for all methods and did not perform any hyperparameter tuning. I would like to argue that this is often a very bad idea leading to incomparable numbers between architectures that are too often not representative of the methods' true performance.
Supplementary Material: I did not read the supplement.
Relation To Broader Scientific Literature: looks good to me, but I am also from the GNN side and not the TDL side.
Essential References Not Discussed: -
Other Strengths And Weaknesses: Strengths:
- relatively easy to read, also for non-experts in TDL
Weaknesses:
- the general construction that is suggested is not highlighted in terms of any structure, its just part of section 4 and the key observation/construction could have been highlighted a lot more. Also an illustration of how any GCN architecture is turned into a TDL architecture could have been nice.
- the experiments (as mentioned earlier)
Other Comments Or Suggestions: none
Questions For Authors: How did you choose datasets and base models?
Would it be possible to re-run the experiments on e.g. molPCBA and malnet-tiny including automatic hyperparameter tuning?
Is it really common that the whole lifting procedure does not help with the performance? As the absolute values reported in table 1 are more or less what one would expect of a pure GNN on the same datasets (at least if there is still data on those).
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your thoughtful comments. We believe they strengthened our work. We are happy to read you found the work accessible for someone not coming from TDL.
**Note on Reviewer's Summary:** GCCNs and TopoTune extend not only GNNs but also non-GNN neural networks. Our framework is also not limited to simplicial and cellular complexes—it generalizes to combinatorial complexes and other higher-order relational structures. While our experiments focus on simplicial and cellular domains, the methodology itself is broadly applicable.
**Responding to performance concerns:** The values in Table 1 serve a benchmarking purpose rather than direct comparison to end-to-end optimized GNNs. TopoBenchmark ensures controlled comparisons by standardizing key components—encoder/decoder design, readout, dataset splits, omission of edge features, and so on. While this impacts absolute performance, it enables a controlled evaluation of architectural differences, where we see GCCNs outperform prior TDL works and standard GNNs when subjected to these constraints.
**Explanation of proofs:** We agree that it is important to briefly describe the idea of the proof. In the updated manuscript, we will add: “Proof of Prop. 4.1 relies on setting the $\omega_\mathcal{N}$ of a GCCN to a simple, single-layer convolution. Proof of Prop 4.2 hinges on the node-wise permutation equivariance of the $\omega_\mathcal{N}$ and the permutation invariance of the inter-neighborhood aggregation. Proof of Prop. 4.3 shows that GCCNs surpass CCNNs in expressivity by relating CCNNs to WL and GCCNs to $k$-WL on augmented Hasse graphs.”
**Weaknesses**
- Beyond section 4, the general construction (GCCNs) are introduced in the introduction as part of the contributions both conceptually and empirically. Introducing them before necessary TDL background is tricky–we would appreciate any input on this. A GCCN is pictured in Fig. 1, showing how it is built from $\omega_\mathcal{N}$ (ex.: GCN, see caption line 70).
- Experiments: We have uploaded an anonymized version of the repository here: https://anonymous.4open.science/r/TopoBench-1F1C/topobench/nn/backbones/combinatorial/gccn.py. Due to the sheer amount of dataset/domains considered, it would be too expensive to run hyperparameter tuning for each of the roughly 50 GCCNs being tested. While we agree tuning would certainly lead to better performance, we argue these results are sufficient to show the superior performance of GCCNs over CCNNs.
**Questions**
1. Addressing in two parts:
- Datasets: The datasets, albeit not recent, were chosen because they are used in TopoBenchmark and thus represent the current norms for benchmarking TDL models. In the future, we will continue testing GCCNs as new datasets inevitably appear in TopoBenchmark. See Q2 for added larger datasets.
- Models: we chose the base architectures largely based on the vanilla GNNs that are often used as inspiration for TDL models. For example, GAT is the inspiration for CAN (Giusti et al.) and GSAN (Battiloro et al. arxiv.org/abs/2309.02138), GCN for SCNN (Maosheng et al. arxiv.org/abs/2110.02585), and GIN for CWN (Bodnar et al., arxiv.org/abs/2106.12575). We aim to show the TDL community how simple it can be to leverage pre-existing infrastructure from the well-established GNN community. We now also include two more recent GNNs (see Q2).
2. We improve the strengths of our empirical results.
- Dataset-wise, we now include 3 larger node-level benchmark datasets (Amazon Ratings, Roman Empire, Minesweeper) that our machine can support memory-wise and that CCNNs have previously been benchmarked on (due to strict word limit here, table can only be in paper). Summary: GCCNs achieve similar performance to regular CCNNs, outperforming them by a significant margin on Minesweeper. We note that all TDL models are constrained by available liftings, as large graph-based datasets significantly increase in size (see arxiv.org/abs/2409.05211 for active research efforts here).
- Model-wise, we now include experiments with GATv2 and PNA in the cellular domain. Results (which we will include in the updated paper) show how the GCCNs built with these models perform consistently well across node-level and graph-level tasks on the cell domain, often <1$\sigma$ of best standard-GNN GCCN, but only outperform them on MUTAG.
3. Lifting generally does improve performance, as seen in comparisons between CCNNs and vanilla GNNs (TopoBenchmark Table 1). We will add a row in our Table 1 showing that standard GNNs match GCCNs/CCNNs in 3 out of 8 datasets, but never outperform them. We also mention very recent work (e.g., Battiloro et al. arxiv.org/abs/2405.15429) showing that simple, general-purpose TDL models outperform GNNs heavily tailored for specific tasks (e.g. molecules).
To conclude, your suggestions helped us summarize theoretical results, contextualize contributions w.r.t. GNNs, and expand our experiments. Please let us know if any concerns remain.
---
Rebuttal Comment 1.1:
Comment: I thank the authors for their detailed and helpful rebuttal and also on the note that the proposed method is more generally applicable than I thought. I also highly appreciate the added experiments on more datasets and stronger base models, I think those will clearly strengthen the paper.
It seems like the dataset complaint is something that is generally problematic in the whole TDL community (but at least the evaluation procedure and train test splits are fixed which was not always the case when those datasets were still in use in the GNN community). I thank you for also providing results on more relevant graph datasets (which for me makes the results a lot stronger as MUTAG, DD, ENZYMES, ... are considered the MNIST of GNNs that are no longer driving research). I sincerely hope that TopoBench is going to improve their dataset assortment soon as more interesting datasets have been driving research in other fields.
This leaves for me mostly the question on hyperparameter tuning and whether a systematic benchmarking approach can exist without it. Personally, I would say that benchmarking is not systematic if hyperparameters are not tuned at all. Since one of the contributions is a systematic benchmarking approach, I feel that this is only partially achieved. For the concrete results, I agree that even without proper tuning, the advantage against other topological models is clear.
In terms of practically usable hyperparameter search, often a simple random search will point at good combinations of hyperparameters making sure that no particularly bad hyperparameter configuration was chosen. If inherently supported by some framework, the additional effort may still be manageable.
---
Reply to Comment 1.1.1:
Comment: We are happy to hear you found our response helpful in better explaining the contribution and the additional experiments to be strong. We sincerely thank you for updating your score to reflect that.
To address the question of hyperparameter tuning: we understand that some amount of traditional tuning is important to any benchmarking system and appreciate the suggestion. We have performed some targeted hyperparameter tuning for a subset of GCCNs (built from GCN and GIN across all neighborhood structures in Table 1) on four datasets lifted to the simplicial domain. Specifically, we focused on hyperparameters that are independent of the base architecture—encoder dropout, encoder hidden features, and learning rate.
Our findings indicate that the best hyperparameter combinations yield results that generally remain within one standard deviation of previously reported values (see tables below). This suggests that tuning these parameters at the GCCN level has limited impact, at least for the values we consider. Optimizing base GNN-specific hyperparameters (e.g., hidden dimensions, dropout) may be more influential, or a more refined strategy of search going beyond systematic grid search of a chosen set of values.
We appreciate the reviewer’s suggestion regarding structured hyperparameter search and its relevance for a practitioner wishing to. apply TopoTune to a real-world scenario. If the paper is accepted, we will explicitly discuss this point and promising directions (ex: GNN level versus GCCN level) for performance gains.
Please let us know if you have any further questions or concerns.
--------
**Table: Hyperparameter search results**
| Model | | MUTAG ($\uparrow$) | PROTEINS ($\uparrow$) | NCI1 ($\uparrow$) | NCI109 ($\uparrow$) |
|---------------------------------|--------------------------|--------------------|-----------------------|-------------------|---------------------|
| Simplicial | | | | | |
| GCCN $\omega_\mathcal{N}$ = GCN | from Table 1 | 74.04 ± 8.30 | 74.91 ± 2.51 | 74.20 ± 2.17 | 75.76 ± 1.28 |
| | best from hyperp. search | 74.29 ± 4.2 | 75.15 ± 2.32 | 73.54 ± 0.14 | 73.04 ± 1.52 |
| GCCN $\omega_\mathcal{N}$ = GIN | from Table 1 | 85.96 ± 4.66 | 72.83 ± 2.72 | 76.67 ± 1.62 | 75.64 ± 1.94 |
| | best from hyperp. search | 83.5 ± 4.51 | 73.56 ± 2.91 | 76.19 ± 1.14 | 75.87 ± 1.62 | | Summary: This paper aims to further topological deep learning by allowing for the easy adaption of any GNN into network for cell complexes. The basis for their method is representing the cell complexes with augmented hesse graphs, running GNNs on these graphs separately and then combining features from each of the graphs
They show that their class of networks has the same expressive power as CCNN, unlike other graph based methods, but allow for easy plug-and-play GNN backbones (on the Hesse graphs). This allows for users to more easily access TDL methods without the loss of expressivity. Although this idea is fairly simple, it has the potential to make a significant impact.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: I skimmed but did not thoroughly check the proofs. I view the theory as fairly "standard"/"unsurpising", but I am reasonably confident it is likely correct (or at least not substantially wrong)
Experimental Designs Or Analyses: I did not check this
Supplementary Material: I skimmed the supplement. The proofs appear properly structured and well organized
Relation To Broader Scientific Literature: This should help accelerate research into TDL
Essential References Not Discussed: None that I am aware of
Other Strengths And Weaknesses: N/A
Other Comments Or Suggestions: N/A
Questions For Authors: Can GNNs that don't fit the strict definition of message passing, e.g. ChebNet be incorporated into your software?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your review. We are happy to read that you believe there is potential for significant impact and acceleration of TDL.
We answer your main question here. Yes, any neural network (not even necessarily a GNN) can be easily incorporated into TopoTune. Practically speaking, as long as the neural network can be imported as a PyTorch module, it can be selected as the chosen base architecture ($\omega_\mathcal{N}$) when defining the GCCN.
As such, selecting a model like ChebNet would simply mean choosing a spectral graph network as the $\omega_\mathcal{N}$ function. In this case, features inside each neighborhood would first be spectrally updated (step B of Fig. 1) and then neighborhood-level features would be spatially aggregated (step C of Fig. 1).
We will better emphasize this fact in the paper at line 324 col 1: “Differently from the work in Hajij et al., 2023, the fact that GCCNs can have arbitrary neighborhood message functions implies that non message-passing TDL models can be readily defined. For example, one could choose $\omega_\mathcal{N}$ to be a spectral graph neural network such as Defferrard et al., 2016.”
Please let us know if you have any other questions. | Summary: The paper introduces Generalized Combinatorial Complex Neural Networks (GCCNs) extending Topological Deep Learning (TDL) models to the combinatorial domain. It generalizes Combinatorial Complex Neural Networks (CCNNs), offering improved expressivity and performance, often with reduced model complexity. To facilitate the design and training of these TDL models, they present TopoTune, a lightweight software framework that simplifies the creation of TDL architectures.
Claims And Evidence: Yes
Methods And Evaluation Criteria: Yes
Theoretical Claims: No
Experimental Designs Or Analyses: Yes
Supplementary Material: No
Relation To Broader Scientific Literature: - This work builds on prior Topological Deep Learning (TDL) work by generalizing Combinatorial Complex Neural Networks (CCNNs), which are more expressive than GNNs.
- The authors prove their method, i.e., Generalized CCNNs (GCCNs) subsume CCNNs, achieving comparable or better performance with lower model complexity.
- The paper introduces TopoTune, a software framework that simplifies the design and training of TDL models, similar to how PyG and DGL standardized GNNs.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: - The paper achieves multi-level information aggregation through an ensemble of augmented hasse graphs. Could a similar effect be obtained using combinatorial or Hodge Laplacians, as explored in https://arxiv.org/pdf/2403.06687 and https://arxiv.org/abs/2309.12971, which aim to integrate information across different ranked simplices via spectral filtering?
- While the proposed Generalized Combinatorial Complex Network (GCCN) is theoretically broad, the experiments are limited to simplicial and cellular complexes—potentially due to memory constraints or challenges in the lifting procedure. Given this, would it be useful to compare GCCNs with models for cell and simplicial complexes, such as MPSN or CWN, to evaluate the method’s efficacy across different topological representations?
- The paper claims to address Open Problem 1 from the TDL position paper. However, the experiments primarily focus on simple graph and node classification tasks, lacking diversity in application domains. This is also valid for open problem 3 as the paper proposes a method not a benchmarking software like TopoBenchmark. The authors should be cautious in making such claims, as the current scope of evaluation may not fully substantiate solving the broader open problem, potentially leading to misleading interpretations.
Other Comments Or Suggestions: See weaknesses and questions.
Questions For Authors: - Are the hyper-parameters of baselines also optimized as they are done for the GCCN?
- How does the transformer version of GCCN compare to this https://arxiv.org/pdf/2405.14094? It seems it has already solved the open problem 11, as mentioned in the TDL position paper.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Thank you for your helpful feedback. We address comments and questions below.
**(Weakness 1) Hodge Theory and Spectral Filtering:** Thank you for your thoughtful comment. While the cited works integrate information across simplices, they are restricted to simplicial complexes due to their reliance on cohomology for defining Hodge Laplacians (not possible for hypergraphs) and the PSD property of Flower-Petals Laplacians (not possible for cell complexes or hypergraphs). Our approach, in contrast, generalizes to diverse higher-order domains without requiring specific spectral notions (e.g., no cohomology theory nor Flower-Petals Laplacian have been developed yet for general combinatorial complexes). However, any spectral model—whether graph-, simplicial-, cellular-, or hypergraph-based—can be used as $\omega_\mathcal{N}$ (step B, Fig. 1) and combined with spatial aggregation (step C). This highlights the flexibility of GCCNs and TopoTune in enabling new topological architectures. We will clarify that spectral networks can serve as base architectures for non-message-passing models.
**(Weakness 2) Experiments in simplicial and cellular domains:** You are correct that we limit our experiments to these two domains in part because of computational cost and in part because of the lack of available “standard” liftings for hypergraphs and combinatorial complexes. However, we do in fact compare GCCNs to existing models by comparing the models to the “Best available model in TopoBenchmark”. These models include CWN and MPSN. In the revised version, we will specify which model is the best available model in TopoBenchmark, and provide a complete list of all models included in TopoBenchmark (and thus that we compare against). We emphasize that the purpose of Table 1 is exactly to evaluate the method’s efficacy across different topological domains, with different choices of base architecture ($\omega_\mathcal{N}$).
**(Weakness 3) Open problems:**
- (OP 1) While we agree the datasets used in these experiments are nothing new, we argue that the unprecedented ease TopoTune provides in defining and training new architectures makes TDL a much more practical option for real-world applications, especially those for which custom GNNs have already been developed. In the updated manuscript, we will rephrase the claim to better emphasize this (line 106, col 2): “Using TopoTune, practitioners can, for the first time, easily define and iterate upon TDL models, making TDL a much more practical tool for real-world datasets (OP 1: need for accessible TDL).”
- (OP 3: need for standardized benchmarking) Our work provides a standardized benchmarking of GCCNs. Unlike traditional studies that tune a single model across datasets, we train ~50 models (varying base architectures and neighborhoods) and compare their performance across multiple datasets and topological domains. This systematic approach is a notable contribution, addressing the field’s reliance on comparisons under heterogeneous training conditions and marking a first step toward solving OP 3. We will clarify this in the contributions: “Unlike prior works that compare models under heterogeneous conditions, our systematic benchmarking provides a controlled evaluation of GCCNs across diverse architectures, datasets, and topological domains.”
**Questions**
1. Beyond the sweep of possible base architectures and neighborhoods, we did not do a traditional “optimization” of hyperparameters for the GCCNs in the sense that we only considered one set of training hyperparameters for each combination of GCCN and task. This set of hyperparameters was selected from the defaults proposed by TopoBenchmark. If there was no default available, we picked the lowest value considered in TopoBenchmark reported grid search. To answer your question, the CCNNs in TopoBenchmark's hyperparameters were obtained with a wide grid search, as described in Appendix C.2 of their work (https://arxiv.org/pdf/2406.06642). We will clarify this in the “Experimental Setup” subsection: “While CCNN results reflect extensive hyperparameter tuning by Telyatnikov et. al, 2024 (see that work's Appendix C.2 for details),...”
2. When we mention OP 11, we are specifically addressing the need for cross-domain attentional TDL. Just like in other areas of TDL, existing attentional works (including Ballester et al) are limited to one domain (in this case, cellular complexes). Because of its integration into TopoTune, the GCCN architecture built with a Transformer base architecture is inherently able to accommodate any topological domain.
Thank you again for your time and review. Your comments helped us clarify our discussion on spectral methods and better articulate the scope of experiments. We have also improved the clarity and nature of our contributions. Please let us know if you have further questions. | Summary: This paper introduces generalized combinatorial complex neural networks (GCCNs), which provide a general technique for turning any existing (graph) neural network architecture into a topological network, which operates on combinatorial complexes. Their method operates by turning a combinatorial complex into a series of graphs, where each one is defined by a neighborhood function of the combinatorial complex. The proposed GCCN is proven to be more expressive than the existing CCNNs, preserves the appropriate permutation symmetries, and also tends to outperform CCNNs on TopoBenchmark graph tasks. In computational complexity, it interpolates between GNNs and CCNNs. The paper also presents a codebase, TopoTune, for implementing GCCNs.
Claims And Evidence: Yes
Methods And Evaluation Criteria: The benchmark dataset makes sense, as well as the comparison to CCNNs. However, it would have also been helpful to compare to non-CCNN baselines, as in the original TopoBenchmark paper.
Theoretical Claims: I did not check correctness of proofs
Experimental Designs Or Analyses: No issues found
Supplementary Material: I skimmed the (full) appendix
Relation To Broader Scientific Literature: This paper builds naturally on Hajij et all, which introduced combinatorial complexes and architectures for them (CCNNs). The new class of architectures, GCCNs, extends CCNNs. It also answers open challenges in TDL as posed by Papamarkou et al 2024. It uses, as a base architecture for the message passing on each created augmented Hasse graph, methods like GIN, GCN, GraphSAGE, GAT, etc, thereby building on those papers.
Essential References Not Discussed: n/a
Other Strengths And Weaknesses: Strengths: The paper is clearly written and outlines their contributions clearly, which is a general architectural framework that seems to address open challenges in TDL. Moreover, the paper produces a library, TopoTune, which promises to be a useful mechanism for fast prototyping of TDL architectures on TopoBenchmark and for reproducing their results with GCCNs. Armed with TopoTune, the experimental results cover a wide range of GCCN architectures, which often outperform existing CCNNs. Although I am not very familiar with TDL, these seems like a valuable contribution to the field.
Weaknesses: The paper only compares GCCNs to CCNNs, rather than other non-topological, perhaps more standard architectures (vanilla GNNs, transformers, etc). Also, their GCCN can be instantiated with many different choices of base graph architecture, but it is not clear how to choose one in practice.
Other Comments Or Suggestions: As someone who is not very embedded in the TDL community, it would expand the reach of your paper to better motivate (briefly) the field of TDL in the intro. The first paragraph does a nice job of this, conceptually; are there empirical works that you can cite, which demonstrate the benefits of capturing these multi-way relationships? For example, what are some datasets on which TDL is SOTA?
Questions For Authors: 1. Is there a reason for only comparing with CCNNs on the tasks in TopoBenchmark?
2. Relatedly, the best MAE reported for ZINC in Table 1 is 0.19. paperswithcode reports the SOTA number as 0.056, as achieved by chromatic self-attention (Menegaux et al 2023), a non-topological or combinatorial architecture. Does GCCN achieve SOTA on any of the datasets in TopoBenchmark, when considering architectures other than CCNNs? If not, how do the authors view the utility of the benchmark, and their GCCN architecture, in a broader context?
3. Based on Table 1, the specific architecture choice of $\omega_{\mathcal{N}}$ that performs best varies by task. In practice, how then should one choose $\omega_{\mathcal{N}}$? Is there any way to avoid exhaustive search and retraining, e.g. by using task-specific insights?
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Thank you for your time as well as your positive and thoughtful review. We are happy to read that the method made sense and the contribution was well justified. We address the raised points about weaknesses and questions below.
**(Weaknesses) Comparing to standard architectures:** We initially only compared GCCN on topological domains for fairness reasons (comparing topological domains amongst themselves), which is why graphs were not included. However, in practice, we completely agree it is very helpful to know if a simple GNN does better. In the updated manuscript, we will add a line to Table 1 that shows the best-performing GNN tested in TopoBenchmark on each dataset. We can then see that standard GNNs achieve comparable results only in 2 of the 16 dataset/domain combinations GCCNs were tested on (PROTEINS in the cellular domain, PubMed in the simplicial domain). This will now be specified in the Results subsection “GCCNs outperform CCNNs.”
**(Weaknesses, Q3) Choosing an optimal base architecture:** You are correct that we do observe significant variation in performance between GNNs (see section “Impactfulness of GNN choice is dataset-specific.”, line 411 col 2, as well as Fig. 5). By better leveraging GNN works in TDL, practitioners can build off the extensive benchmarking work performed in the GNN field (see for example the benchmark study https://arxiv.org/abs/2003.00982). For example, it comes as no surprise that the base architecture of GIN is a good choice for the ZINC dataset, as that is how it appears in the GNN world as well. We leave the study of further pre-training optimization of hyperparams such as choice of topological domain and choice of neighborhoods to future work. However, we emphasize that one of the goals of a principled framework like TopoTune is to make such a study, that would be otherwise extremely hard, feasible.
**(Comments) Better motivating TDL:** TDL architectures perform well in general but are particularly valuable when higher-order multiway interactions matter significantly. Examples include citation networks (Battiloro et al., https://arxiv.org/abs/2309.02138) and human skeleton-based action recognition (Hao et al., https://ieeexplore.ieee.org/stamp/stamp.jsp?tp=&arnumber=9329123). A notable SOTA TDL model is TopoRouteNet, used in computer network modeling (Bernardez et al., https://arxiv.org/html/2503.16746v1). Recent work (Battiloro et al., https://arxiv.org/abs/2405.15429) also highlights TDL’s potential in molecular tasks, demonstrating that simple, general-purpose TDL architectures can outperform models heavily tailored for molecules. That said, benchmarking our methods on similar datasets to prior works is a crucial step toward broader application-specific adoption. We will add a note on successful TDL applications at the end of the “TDL Research Trend” section of the introduction.
**Choosing tasks (Q1).** TopoBenchmark consolidates the most commonly used benchmark tasks in TDL, as well as the highest-performing, most well known models in TDL. By including this variety of tasks, GCCNs benefit from a comprehensive test against the field. Going beyond that, we also specifically use the TopoBenchmark platform to ensure fair comparison amongst architectures, as all the tasks are homogenized in, for example, data split, reported performance metric, and so on (see point below).
**SOTA Results (Q2).** This performance gap on ZINC primarily arises from the benchmarking framework used in our work. As TopoBenchmark (Telyatnikov et al.) standardizes several components—such as encoder/decoder, readout, dataset splits and the omission of edge features—it ensures a more controlled comparison of model backbones but may come at the cost of absolute SOTA performance. Generally, high-performing GNN models, including Chromatic Self-Attention (Menegaux et al. 2023), are designed as end-to-end architectures with carefully tuned encoders and readouts, whereas TopoBenchmark enforces uniformity in these components to isolate and assess the impact of architectural differences.
In this context, while GCCN may not achieve SOTA performance, the benchmark enables meaningful insights into the role of topological architectures by minimizing confounding factors. This approach aligns with our broader goal: rather than optimizing for peak performance on individual datasets, we aim to establish a fair and standardized evaluation framework that can help guide future architectural improvements. Importantly, TopoBenchmark is flexible enough to accommodate advances in GNN design. This could look like building a GCCN with Chromatic Self-Attention as a base architecture ($\omega_\mathcal{N}$).
**Conclusion.** Thank you again for your review. Your feedback helped us make (key) comparisons to GNNs, better motivate TDL, and improve our contextualization of results. We appreciate your insights and believe they have made the manuscript stronger. | null | null | null | null | null | null |
Softmax is not Enough (for Sharp Size Generalisation) | Accept (poster) | Summary: This paper can be divided into 3 parts:
1) The observation and proof that softmax-based architectures (such as Transformers) will have a "dispersion" phenomenon when tested on longer inputs than they are trained on.
2) The observation that this dispersion phenomenon can degrade the length-generalization performance of transformers on simple algorithmic tasks such as finding the maximum element in a list.
3) An ad hoc "adaptive temperature sampling" scheme that seeks to remedy the dispersion phenomenon and leads to performance improvements on the "maximum element" task and on several problems in the CLRS-text benchmark.
Claims And Evidence: The proofs are clear.
Methods And Evaluation Criteria: Yes, these make sense.
Theoretical Claims: Yes, I checked the main theorem and its proof.
Experimental Designs Or Analyses: Yes, I checked the experimental details for the maximum task and the CLRS-text task and they seemed ok to me. The adaptive temperature scheme is arguably very ad hoc, but it seems to give some small gains.
Supplementary Material: Yes, I reviewed Appendices A-D.
Relation To Broader Scientific Literature: The paper's observation is simple, but thought-provoking. The maximum-element task is a convincing illustration that this dispersion phenomenon in LLMs is real and could be one of the barriers to length generalization. On the other hand, the adaptive temperature sampling scheme is less convincing, more ad hoc, and leads to seemingly small gains on the problems tested. Therefore, I overall find highlighting the dispersion phenomenon to be the more valuable contribution in this paper, since it may well motivate future work on this topic.
Essential References Not Discussed: Not insofar as I know
Other Strengths And Weaknesses: I had some trouble following the explanation of the adaptive temperature sampling scheme.
Other Comments Or Suggestions: The paper is written in a somewhat informal style, which I am fine with because it is mostly clear. However, in particular this sentence could be improved: "We prove this important result now" before Theorem 2 could be changed to simply read "We prove this result now".
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer n5x1,
We are highly pleased to read your review, and really appreciate your positive view on our results and their significance!
In what follows, we reply to all of the points you raised:
> On the other hand, the adaptive temperature sampling scheme is less convincing, more ad hoc, and leads to seemingly small gains on the problems tested. Therefore, I overall find highlighting the dispersion phenomenon to be the more valuable contribution in this paper, since it may well motivate future work on this topic.
We fully agree with you that the key outcome of our work should be highlighting the dispersion effect, improving understanding of it, and stimulating future work towards addressing it. Adaptive temperature was designed as a mostly ad-hoc method to illustrate that even simple interventions can counter dispersion in a way that leads to measurable improvements, but it does not escape the confines of our theoretical results – as we clearly highlight in our Conclusions.
> I had some trouble following the explanation of the adaptive temperature sampling scheme.
We appreciate this remark and commit to adding a new section (potentially in the Appendix) which will provide a step-by-step overview of how the sampling scheme was arrived at.
> However, in particular this sentence could be improved: "We prove this important result now" before Theorem 2 could be changed to simply read "We prove this result now".
This is a great suggestion, and we will tone down by removing the word ‘important’ here. | Summary: The function softargmax (commonly referred to as softmax), which is used to create probability output vectors and attention heads within neural networks, becomes less like argmax (less sharp) as the number of elements over which the softmax is applied increases. This is detrimental for learnt circuits within transformer architectures that need sharp attention, especially when deployed at inference time on longer sequences than presented during training.
Claims And Evidence: The proofs given in Lemma 2.1 and Theorem 2.2 are rather weak with respect to the arguments made in the paper. For example, Lemma 2.1 assumes that logits are bounded below by $m$ and above by $M$, both of which are finite values, and provides a proof for the limiting case $n\to\infty$. This is an incredibly loose bound. The experiments in the paper go up to $n=16,384=2^{14}$, while machine precision limits would only provide a lower bound of $m=-10^{38}=-2^{126}$, so this sequence length and lower bound is going to induce minimal dispersion on the attainable sharpness. The proofs provided by the authors demonstrate that softmax must disperse in the limiting case, but not that it does in practice for the scales actually used with transformer models.
The authors also included empirical studies (Fig 2 and 3), where a model is tasked with identifying the maximal element in a sequence, which I appreciated. However, I think it would help support the paper if there were additional empirical measurements. For example, what is the distribution of logit values seen in LLM attention heads at inference time across a range of tasks? The minimum and maximum values from this would be informative to establish a practical range for $m$ and $M$.
Additionally, I think there could be more discussion on the factors which prevent the model from achieving an arbitrarily sharp distribution (e.g. label noise prevents the model from learning arbitrarily large parameter values; the derivative to make off-target logits arbitrarily negative can vanish when the softmax output is already sufficiently sharp).
Methods And Evaluation Criteria: Yes.
Theoretical Claims: The proofs in the main paper (Lemma 2.1, Theorem 2.2, Prop 3.1, Prop 3.2) are correct.
Experimental Designs Or Analyses: For the experiments comparing the adaptive-$\theta$ model presented by the authors against the baseline model for the max task (Table 1), I think these results could be usefully expanded by including additional "oracle" measurements which use the optimal theta at inference time. This will help to indicate how much of the possible gains which could be attained by only changing the temperature were achieved by the adaptive temperature.
The discussion of the comparison for the adaptive-$\theta$ method introduced in the paper (Fig 8.) could be more detailed. In particular, some tasks see the adaptive temperature model perform worse than the baseline (namely heapsort, mst kruskal, and bubble sort). I would appreciate if the authors could comment on whether this deficiency is meaningful, for instance are there some features these tasks have in common which makes adaptive-$\theta$ perform poorly here? Is it just because adaptive-$\theta$ was fit on the max task and does not generalize well to these tasks?
Supplementary Material: Appendix A.
Relation To Broader Scientific Literature: The issue of softmax dispersion is already known within the community broadly speaking, but I appreciate that this work presents the problem well and raises awareness of this issue.
Essential References Not Discussed: Not that I am aware of.
Other Strengths And Weaknesses: None.
Other Comments Or Suggestions: **Figure 5.**
The title and y-axis indicates that in half the domain you are dividing the logits by a negative number, which doesn't make sense w.r.t. the meaning of temperature. I suggest this is refactored. The implication is more like the sequence is changed by negation rather than the temperature adjusted. But the sequence is controlled by lambda on the x-axis, so it is odd to have two different sequences stacked one above the other and joined at the $\theta=0$ line To be honest, I am not sure what I am supposed to learn from this figure anyway. Is this power series supposed to be indicative of real data? If so, then how is it related to real data?
The "jet" colormap used here is not perceptually smooth. Its use creates the visual appearance of discontinuities at the luminosity inflection points (e.g. yellow and cyan). I recommend using a more modern colormap instead. There is a good reason why the defaults in matplotlib and MATLAB have both moved away from jet several years ago. Seaborn throws an error if the user requests to use jet, rather than comply. There are many resources which have published which discuss the issues with jet, e.g.
- https://www.youtube.com/watch?v=xAoljeRJ3lU
- http://jakevdp.github.io/blog/2014/10/16/how-bad-is-your-colormap/
If you like jet because it breaks the data down into blocks of distinct colours and feel that the new colormaps with smooth luminosity changes (e.g. viridis) are too smooth making them hard to read, then you should be breaking the data up into discrete colours with intentionality, rather than as the side-effect of a poor colormap. In this case, you should use a contour plot, either with contour lines or with discrete blocks of ~24 colours, instead of a smooth colormap.
**Typos and snags.**
- L018 "circuits" incorrect quote mark
- L055 right column, missing word "A strong current [topic] in this space"
- L073 right column, it would be helpful to know how samples are OOD for this point (i.e. is it OOD in sequence length or not, as that is pertinent to the topic of the paper)
- L105 right column, "a collection of [n] nodes" as n is the number of nodes, not the label of the collection.
- L112 The notation is a bit confusing since k_i and v_i are vectors instead of elements within vectors.
- L124 Eq 3, suffix variable `j` should be `i`
- Eq 3, 4. Adding a comma between equations on the same line may help delineate between them.
- Fig 1: It appears that the caption text colours are intended to indicate the block types within diagram. However, the token and MLP colours are too similar in the figure and the text colours are not quite the same shades as the figure colours. I thus recommend the authors add labels within the figure, and/or describe the colours in the caption to make the reference clear.
- Fig 2: What's the number of items used in the base case? Please add this to the caption.
- Fig 3: Add units for y-axis (presumably bits)
- Fig 4: ~L222 "see Figure 5" should be "see Figure 6"
- Tab 1, L382: There shouldn't be a space after the thousands separator, having this in makes the numbers harder to read.
- Fig 8: Some tasks have the adaptive temperature model worse than the baseline (heapsort, mst kruskal, bubble sort) Can the authors comment on what features these tasks possess
- Fig 8: Legend should be at the bottom of bridges or activity selector instead of the top of bfs so it doesn't obstruct data.
- L692: Usually it is just called the Adam optimizer, not the Adam SGD optimiser. Referring to it as such may cause confusion.
- L654: Hard-written "Equations 2--3" is incorrect and should be replaced with actual equation numbers as reference.
**Citations:**
- Be careful with protecting casing of acronyms.
- L462: "Transformers need glasses! information..."
- L497: "clrs"
- L583: "gpt-2"
- Please consider adding links to references which currently don't have one. This makes it easier for a reader to navigate to the cited works. You appear to have your arXiv references set up in a consistent manner, so adding either a URL or a DOI field can be done automatically for these with a regex call.
Questions For Authors: None.
Code Of Conduct: Affirmed.
Overall Recommendation: 4 | Rebuttal 1:
Rebuttal: Dear Reviewer jdu5,
Thank you so much for the very careful review and the vast amount of useful suggestions for improving our work! We are very happy you appreciated our efforts to raise awareness of the dispersion issues of `softmax` in the ICML community!
We provide detailed answers to your comments below, and we hope they will be to your liking.
### **Bound looseness**
We highly appreciate your remark about the looseness of our bound, and wholeheartedly agree it is worth discussing in more depth. We stratify our answer by your specific comments, and commit to updating the paper to incorporate all aspects of our discussion!
> The experiments in the paper go up to n=16,384=2^14, while machine precision limits would only provide a lower bound of m=−10^38=−2^126, so this sequence length and lower bound is going to induce minimal dispersion on the attainable sharpness.
Just to assert our understanding: due to the exponents you presented, we find it likely that your bounds were derived under the assumption of the `bfloat16` type being used. This is a fair assumption, though we remark that large-scale frontier models are frequently served at even lower-precision types – sometimes with aggressive quantisation. This might well affect the _practical_ lower bound obtained for $m$ due to machine precision.
> The proofs provided by the authors demonstrate that softmax must disperse in the limiting case, but not that it does in practice for the scales actually used with transformer models.
In this regard, it is worth taking Theorem 2.2 together with Proposition 3.1, which shows models aiming to improve sharpness have no choice but to _amplify their weights_ at some point in the architecture, and that the weight magnitudes directly control the empirically observed values of $m$ and $M$. But amplifying weights is generally risky due to the danger of overfitting—as such, the model has no choice but to keep the empirical spread somewhat contained. This immediately brings us to your next point:
> For example, what is the distribution of logit values seen in LLM attention heads at inference time across a range of tasks? The minimum and maximum values from this would be informative to establish a practical range for m and M.
This is a fantastic suggestion and we really appreciate it!
To measure this, we fed an entire code sample of Gemma’s Modules file (available at https://github.com/google-deepmind/gemma/blob/main/gemma/modules.py, ~4,000 tokens) to Gemma 2B and 7B models. The empirically observed values of the logit spread, $\delta = M - m$, across all attention heads, were as follows:
| **Model** | **Average** $\delta$ | **Maximum** $\delta$ | **Minimum** $\delta$ |
| :------- | :----------------------: | :-------: | :--------: |
| Gemma 2B | 5.69 ± 2.05 | 14.78 | 2.28 |
| Gemma 7B | 5.82 ± 2.61 | 32.74 | 0.09 |
This shows that empirical logit spreads in practical queries are, even in their maximal occurrence, rather small compared to the machine epsilon-induced bounds mentioned before, and should give further credibility to the practicality of our results. We of course will include this table in the paper!
> Additionally, I think there could be more discussion on the factors which prevent the model from achieving an arbitrarily sharp distribution
Another excellent proposal – we fully agree with all of your specific factors, and will make sure to thoroughly discuss those in our revision.
### **Specifics of Adaptive-$\theta$**
As suggested, we have performed preliminary experiments with a custom oracle multiplier for Adaptive-$\theta$. While this led to (2–3%) percentage point improvements on lesser OOD sizes, there was no consistent improvement on longer sequence lengths.
We are also happy to enrich the discussion of the comparisons in Figure 8. While we cannot make very strong claims, a unifying property of Heapsort, MST Kruskal and Bubble Sort in CLRS-Text is that they all occupy relatively large chunks of Gemma 2B’s context window, which stretches further beyond the largest contexts over which the polynomial fit of Adaptive-$\theta$ was fit—and this might cause an unintended shift, which is in line with your suggestion.
### **On Figure 5**
* We acknowledge your point regarding `jet`. We agree that perceptually uniform colormaps like `viridis` or `plasma` offer better visual representation, and will switch!
* We used power series (controlled by $\lambda$) as a simple model to represent sequences with varying degrees of "sharpness" in their logit distributions.
* While negative $\theta$ does not have a direct thermodynamics meaning, it allows us to explore the behavior of the `softmax` function beyond the typical regime.
### **Miscellaneous issues**
We are very grateful for your thorough comments about several miscellaneous minor issues in the paper. We fully agree with your remarks, and commit to correcting them in our revision.
---
Rebuttal Comment 1.1:
Comment: I am glad to hear my constructive feedback was well received!
To a first order approximation, logits within neural networks are typically distributed like a standard normal distribution. So an average delta around 6 is what I would intuitively expect, and the reason why the issue of the dispersal is intuitively salient. I was of course being somewhat flippant when I referred to machine precision limits setting a lower bound for m: the problem was that the typical values for m and M or delta were not discussed in the paper, so the scale of the issue of the dispersal was not made as clear as it deserved. I appreciate the addition of the measurements made on the Gemma code base, but to better integrate the measurements I encourage the authors to measure the delta observed with stock Gemma models on CLRS-Text as well.
**Figure 5**
> We used power series (controlled by $\lambda$) as a simple model to represent sequences with varying degrees of "sharpness" in their logit distributions.
> While negative $\theta$ does not have a direct thermodynamics meaning, it allows us to explore the behavior of the softmax function beyond the typical regime.
I still think I would prefer to see this figure as four subplots, $\pm(\lambda^{\pm i})/\theta$ where $\lambda \ge 1$, $\theta \ge 0$, $i \in [1, \cdots, 10]$. This clearly delineates the four regimes which are being considered:
- $+(), +i$: power series where smaller terms are high density and big terms are low density
- $-(), +i$: power series where small terms are low density and bigger terms are high density
- $+(), -i$: power series where small terms are low density and bigger terms are high density, and everything is near 0
- $-(), -i$: power series where smaller terms are high density and big terms are low density, and everything is near 0
As the authors have addressed my critique sufficiently, I have raised my score.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer jdu5,
Thank you so much for acknowledging our efforts and raising your score!
We completely share your motivation about the utility of reporting the empirical delta values and will report them for CLRS-Text as well.
Your suggestion about four subplots makes sense and we will amend the figure accordingly.
Best,
Authors | Summary: The authors argue that modern deep learning architectures are fundamentally incapable of learning sharp functions(for example, max) due to the disperse nature of the softmax function in out-of-distribution settings. In addition, the authors propose an adaptive temperature mechanism as a plug-in technique at inference time for improving the sharpness.
Claims And Evidence: The authors argue about the limitation of the softmax function and provide both theoretical and empirical evidence for it.
The authors also provide theoretical and empirical visualization to support adaptive temperature.
Methods And Evaluation Criteria: Both the argument around the softmax limitation and the proposed method make sense.
However, the evaluation is rather "toy". I understand that max retrieval provides a clean setting. However, only CLRS-Text makes it hard to understand the usefulness of adaptive temperature or the problem from the dispersed nature of softmax in the real world.
Theoretical Claims: I checked Lemma 2.1 and Theorem 2.2, which seem correct.
Experimental Designs Or Analyses: I checked the settings for max retrieval and CLRS-Text, and the experimental design and analysis make sense.
Supplementary Material: I review Appendix A to understand max retrieval settings.
Relation To Broader Scientific Literature: The limitation on softmax and adaptive temperature is relevant for the boarder audience, given the prevalence of softmax in modern ML systems.
Essential References Not Discussed: I am not an expert on theoretical work around softmax or out-of-distribution. However, the discussion on the background, primer on attention heads and transformer, and related work on adapting temperature seem complete to understand the problem and proposed method.
Other Strengths And Weaknesses: I think the primary significance of this paper lies in the discussion on softmax limitation. My main concern is discussed in the evaluation criterion area.
Other Comments Or Suggestions: None
Questions For Authors: 1. The authors clearly discuss the disperse problem of softmax function. I wonder how big the problem is when we zoom out to the entire transformer, given all the residual connections and normalization etc?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer 5ZBY,
Thank you for your careful review and the positive assessment of our contribution! We are very grateful for your comments, and provide our responses below – hoping that they are to your liking!
> The authors clearly discuss the disperse problem of softmax function. I wonder how big the problem is when we zoom out to the entire transformer, given all the residual connections and normalization etc?
This is an excellent question!
We study exactly this, to varying extents, in **Appendix B** and **Appendix C** of the original submission. We provide a brief summary of these results for your convenience, and are very happy to discuss them further:
* [Corollary B.1] We prove that the dispersion effect necessarily leads to classification failures in a single-layer Transformer architecture on simple reasoning tasks (such as predicting the maximum).
* [Remark B.2] We make an informal sketch of how Corollary B.1 can be extended to deep Transformer architectures (both BERT- and GPT-style) to show the same kind of classification failures must occur past a certain number of input tokens. This argument explicitly takes into account residual connections.
* [Remark C.1] We prove that, in BERT-style Transformers without residual connections, the situation is particularly dire: when a particular layer disperses, **all** layers after it will be immediately dispersed as well.
The residual connections play an important role with depth, as evidenced by Remark C.1: they allow a model to “shortcut” a dispersed layer and retain its original embeddings for longer. However, Theorem 2.2 shows that, no matter how many residual connections are used, each individual layer still must disperse past a certain size.
The normalisation layers often play a counter-productive role, which we discussed in Section 3: they _clamp_ the input to a certain expected norm, meaning that there is higher pressure on key/query matrices ($\mathbf{K}$, $\mathbf{Q}$) in order to achieve a sufficient logit spread (cf. Proposition 3.1).
> However, the evaluation is rather "toy". I understand that max retrieval provides a clean setting. However, only CLRS-Text makes it hard to understand the usefulness of adaptive temperature or the problem from the dispersed nature of softmax in the real world.
Thank you for your remarks! Since our study concerns out-of-distribution generalisation specifically, we have focused our analysis on tasks requiring out-of-distribution generalisation (such as CLRS-Text, a collection of thirty challenging algorithmic execution tasks across many problem sizes). In most other static benchmarks, it might be very difficult to measure the distribution shift in the test set.
We also remark that focusing on synthetic execution tasks is the standard approach in papers studying length generalisation in LLMs. As a standard representative we refer to “Exploring Length Generalization in Large Language Models” (Anil et al., NeurIPS’22), which studies only two synthetic problems: parity and variable assignment. In contrast, CLRS-Text studies thirty such problems, with a significant increase in their complexity. | Summary: This paper studies the *sharpness* of the softmax function from a *size generalization* perspective. The authors regard a function as being **sharp** if its output can be expressed using a constant number of inputs. The authors refer as **size generalization** the study of what happens when the function is subject to a larger number of inputs. In this paper, the authors argue that using an adaptive temperature parameter can help preserve sharpness by lowering the temperature enough to reduce entropy while maintaining the trained model accurate. More generally, the authors argue in their main theoretical results that it is not possible to preserve the sharpness of the softmax function as the number of inputs grows arbitrarily large.
Claims And Evidence: My main concern with this paper is not correctness, but rather significance: the theoretical results claimed do not seem surprising or nontrivial to prove for someone working on that line of inquiry. From the examples at the top of Page 2 that the max function is sharp and the average function is not sharp, the fact that softmax is not sharp for an arbitrarily large number of inputs seems evident and proving that result seems in line with a doctoral-level homework exercise.
Moreover, if we are to assume that softmax is sharper with smaller inputs or subject to a lower temperature parameter, then I believe that we lack a definition for proper theoretical discussion: there should be a threshold for the minimum contribution of an input to consider it relevant to the output of the function (and possibly how many inputs significantly contributing to the function output is too many). Otherwise, any contribution of an input should be counted, and then softmax is trivially not sharp.
More generally, any discussion about models when their dimensions tend to infinity changes the nature of the beast. For example, arbitrarily deep or wide neural networks may hold properties that a finite neural network architecture cannot promise. Hence, I believe that the proper framing here should have been about scaling up sharpness with respect to input size - and how to overcome the challenges associated with that.
Methods And Evaluation Criteria: See item above.
Theoretical Claims: See two items above.
Experimental Designs Or Analyses: See three items above.
Supplementary Material: No.
Relation To Broader Scientific Literature: I am not sufficiently familiar with the line of work to which this paper contributes to make a comment on this.
Essential References Not Discussed: I am not sufficiently familiar with the line of work to which this paper contributes to make a comment on this.
Other Strengths And Weaknesses: Strength: the authors have a clear writing and frame well some interesting aspects of the theoretical work around attention. I am curious to read more about it following their description.
Weakness: I personally find the terminology "reasoning device" speculative. I would recommend making the discussion more objective without such and related terms.
Other Comments Or Suggestions: The use of rephrasing in theoretical statements (the "That is" in Lemma 2.1, Theorem 2.2, and Proposition 3.1) is not adequate. If needed, those can be added either before or after the formal statement (or after the proof), but not in it.
Drawing conclusions inside a theoretical statement (the "Thus" in Proposition 3.2) is not adequate. If relevant, that part should have been a separate corollary after the parent result.
Abstract:
- ' "circuits" ': replace '' with `` before this word
Page 1:
- "does not have a chance": too informal
Page 4:
- In the proof of Theorem 2.2: "for [some choice of] constants $m$ and $M$"
Questions For Authors: By the last paragraph of Section 2, my impression is that the whole argument of this paper is that there are clear limits to the transformer architecture if taking arbitrarily large inputs. Is that the case, or do you believe that there is a better function than softmax for the purpose that it serves?
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: Dear Reviewer WiLd,
We would like to thank you for carefully considering our paper. While we regret that your initial rating of our paper was negative, we believe you raised important points and that there is a clear discussion to be had, and that we may be able to provide relevant arguments for you to reconsider the relevance of our work.
To that end, we address all of your points in order:
### **On significance of our results**
We do not dispute that this result was not very difficult to prove, but we argue that it is definitely **not** evident to a significant part of the ICML community. And we hope you agree we should preferably judge proofs’ significance using the latter criterion rather than the former -- simplicity is not in and of itself bad.
Therefore, we will focus this part of the response on discussing whether our results are evident.
Due to the anonymous nature of the reviewing process, the only concrete evidence we can provide towards this are the reactions of the other three reviewers:
* [Reviewer n5x1] _The paper's observation is simple, but thought-provoking._
* [Reviewer jdu5] _I appreciate that this work presents the problem well and raises awareness of this issue._
* [Reviewer 5ZBY] _The limitation on softmax and adaptive temperature is relevant for the boarder audience, given the prevalence of softmax in modern ML system_
We wish that we could provide more concrete evidence, but we cannot for obvious reasons. Suffice it to say, we have had numerous discussions with our previous collaborators (who are at many varying levels of seniority and expertise about self-attention) about this result, and the overwhelming majority of them initially reacted to our result with **surprise**; i.e., not expecting that the dispersion effect is guaranteed in `softmax`. In fact, it was exactly these interactions that compelled us to write this paper in the first place!
It is interesting to ponder why our result is surprising to such a broad audience of AI researchers. Our hypothesis is that this is due to several current trends:
* The overall prevalence of the Transformer architecture and the many expressivity results for it;
* The elevated importance of the dataset for training AI models, and the diminished importance of architecture choice;
* Mechanistic interpretability research, which reverse-engineers sharp behaviours in trained LLMs.
Such trends may easily lead to a naïve intuition that `softmax` should **always** be able to pick out the key elements / circuits to apply to the data, so long as we choose the “right data” to train on.
However, the _length generalisation_ setting challenges this preconception, because it by default focuses on evaluating beyond the largest training data point. Further, mechanistic interpretability research typically does not operate in such regimes, and the circuits discovered therein do not generalise to ever-increasing inputs.
We believe our paper plays an important part in grounding the limitations of the `softmax` function, especially when considering how it is leveraged in modern LLMs. We hope you will agree with this motivation!
### **On thresholding contributions**
We appreciate your comment and believe addressing it will improve the rigour of our argument! In our revision, we will explicitly mention thresholding contributions when defining sharpness, and how our Theorem 2.2. proves that no fixed threshold ($\epsilon > 0$) is sufficient to maintain sharpness on larger inputs.
### **On the infinity dimensions and the ‘scaling up sharpness’ framing**
To be clear, our work does not assume infinitely deep or wide architectures. We start with the practical assumption of a model of fixed depth & width, and then quantify how its coefficients’ sharpness decays with respect to input size – exactly as you suggested. We commit to adding further sentences around the problem description to make this crystal clear.
### **Improvements to `softmax`**
Our argument is slightly more nuanced than what you suggested. We suggest that it is the _combination_ of the `softmax` function _and_ how it is used within Transformers (e.g. tokenisation, global attention, etc.) that causes limitations over arbitrarily large inputs. That is, certainly the Transformer itself could be improved, but there are also possibilities of improving the `softmax` function itself.
We cited several examples of possible alternative aggregation functions in the Conclusions: linear attention, sigmoidal attention, and stick-breaking attention. There are also proposals such as selective attention (Leviathan et al.), which retain `softmax` but modify the algorithm which allocates logits in a more size-robust manner. For several of these proposals, Theorem 2.2 would not apply.
We are happy to add this discussion to the revised paper!
### **Miscellaneous issues**
We are happy to correct all minor nits you pointed out, as well as avoid usage of terms like ‘reasoning device’ in a revised paper.
---
Rebuttal Comment 1.1:
Comment: Given the argument of the other reviewers about the relevance of the paper to the community, I will update my score. I hope that the authors make the paper a little more clear and precise, as requested in my review.
---
Reply to Comment 1.1.1:
Comment: Dear Reviewer WiLd,
Thank you very much for taking our response into consideration and improving your score!
> I hope that the authors make the paper a little more clear and precise, as requested in my review.
We reiterate our full commitment to incorporating all the clarity and precision changes you requested, along with any other opportunity we find for doing so.
Best,
Authors | null | null | null | null | null | null |
SAE-V: Interpreting Multimodal Models for Enhanced Alignment | Accept (poster) | Summary: The paper proposes SAE-V, a framework that utilizes SAEs trained on top of multimodal large language models (MLLMs) to measure image-text alignment. Specifically, for a given SAE feature, it retrieves the top activating tokens and image patches and computes their cosine similarity score, which produces an alignment metric for a single dataset sample. The paper evaluates this metric for applications like image patch filtering and dataset filtering.
Claims And Evidence: - Claim 1. SAE-V is superior to SAE in reconstruction quality.
- The presentation of this section should be improved; it is hard to evaluate the validity of the claim without further explanation.
- Figure 3 is missing a description of SAE vs. SAE-V. Is it that SAE is trained only on text features while SAE-V is trained jointly on text and image features? Is SAE evaluated on both text and image features, or only on text features? I don’t understand “Original” — shouldn’t the original feature achieve a reconstruction loss of 0?
- Claim 2. SAE-V can be used for image patch filtering.
- This experiment is quite novel and interesting, but more details could be provided.
- In L265, how is this evaluation performed? What is the size of the ImageNet test set, what MLLM is being evaluated here, how is it being evaluated (is it a comparison between the MLLM output vs. the ground truth ImageNet class)? In Figure 6, the y-axis is labeled as “loss value” but the caption states that it is “classification accuracy” — what is being plotted here? How is the masking performed; are the features of those image patches just zeroed out?
- Claim 2 and 3 are also missing a comparison against the non-SAE baseline. For example, you could compute the alignment metric by computing the cosine similarity of the original text token and image patch features, without any SAE projection. This would better illustrate why SAE-V training is necessary, beyond a simple training-free baseline.
- Claim 3. SAE-V can be used for dataset filtering.
- The experiment is well motivated and interesting, but the presentation is confusing.
- In Figure 7, what is the performance score metric exactly — is it some classification accuracy or a loss value? While it is trained on Align-Anything, is it also evaluated on a held out subset of Align-Anything, and what is the size of this subset? The figure caption states that the y-axis is scaled according to the “full dataset’s performance” — why at the 100% data percentage is the performance score ~96%, not 100%?
- For the comparison in L371, beyond IFD I would recommend the paper also include a CLIP baseline (i.e., taking the top percentage of samples based on highest CLIP scores). This CLIP baseline is already explored in prior work such as in [1]. To this end, I would also disagree with L375, which states there are “no widely recognized data filtering methods specifically designed for multimodal data.”
[1] Gadre et. al., 2023. DATACOMP: In search of the next generation of multimodal datasets. NeurIPS 2023.
Methods And Evaluation Criteria: See “Claims And Evidence” above.
Theoretical Claims: N/A
Experimental Designs Or Analyses: See “Claims And Evidence” above.
Supplementary Material: Yes, I looked at the Supplementary.
Relation To Broader Scientific Literature: The paper proposes a novel use case for SAEs for measuring image-text alignment in multimodal models. To this end, they also introduce image patch filtering and data filtering as evaluation tasks. Both the method and evaluation tasks have not been explored in the context of MLLMs.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: Strengths
- The proposed alignment score is well-motivated and interesting.
- The proposal of image patch filtering as an evaluation task is very unique and compelling. Future work in multimodal alignment would also benefit from this framework.
- The dataset filtering evaluation is sensible and a practical example of how SAE-V is useful.
Weaknesses
- The presentation of the experiments needs a lot of work. Many of the figures and experimental setup are unclear and missing key details; also see “Claims And Evidence” above.
Overall, I like the premise of the paper but the presentation is poor. I am open to revising my score if the authors are able to address my questions and clarify details regarding the experiments.
Other Comments Or Suggestions: - L160 typo, “donated” should be “denoted”
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Your suggestions are insightful and will enhance the completeness of our paper!
We used all available resource and devoted efforts to conduct additional experiments. We addressed all your negative comments below and will add them into the revision. **If this rebuttal addresses your concerns, we earnestly ask you to consider raising the score and supporting us for acceptance.**
## Claim 1 & Weakness: We prune the overall presentation of the paper to reduce repetitive expressions and add necessary backgrounds.
Limited by the length of rebuttal, we are not able to list all the changes we made, so only key examples are provided. E.g.:
- line 245-253:
> The transferability of SAEs between foundation models and instruction-tuned models has been extensively investigated in text-only contexts[3][4][5], as it demonstrates whether SAEs can capture universal semantic features within LLMs. Similarly, the transferability from MLLMs to corresponding LLMs serves as a critical metric for the quality of features learned by SAE-V.
> (Followed by original content)
- Fig. 7 caption:
> We evaluated SAE-V data filter method on LLaVA-NeXT-7B model, Align Anything dataset, and LLaVA-Bench benchmark. The result show that all SAE-V-based methods significantly outperforms the random selection baseline, while the cosine similarity filter achieved 108% of the full dataset’s performance with only 20% of the data, and the co-occurrence filter peaked at 50% of the data, reaching a score of 108.17.
To address the specific concerns:
- SAE only accepts textual tokens, while SAE-V is designed for both text and image tokens. When evaluating with multimodal input, SAE can only reconstruct text features, whereas SAE-V reconstructs both text and image features, achieving lower reconst. loss (Fig. 4, Col. 3). Moreover, even when evaluating on text tokens, SAE-V surpasses SAE in reconstruction capability (Fig. 4, Col. 1-2), showing effective cross-modal generalization.
- Regarding the "Original" bar in Fig. 3: The reconst. loss measures how well the model predicts the next token compared to ground truth. The original model's predictions are also probability distributions, not exact predictions, which is why the "Original" has non-zero reconst. loss.
## Claim 2: We provided additional details, and conducted extra ablation study to compare SAE-V with non-training baseline.
Regarding details of the experiment in Section 3.2:
- **Pipeline:** Given the 1000 val. set of ImageNet, We score the 24\*24 image patches according to the metrics of SAE-V features (Fig. 6 legend). We filter out the patches according to the score and the given ratio (x-axis in Fig. 6). We use LLaVA-NeXT-7B to classify the filtered image, and calculate the accuracy (Not loss value) of LLaVA-NeXT-7B output as y-axis in Fig. 6.
- **Target:** This experiment is designed to support the claim that SAE-V could preserve the key info from images, and the higher accuracy is, the more key info is preserved through the leftover patches. E.g., in Fig. 5, SAE-V could preserve the most relevant information (the dog) in the image.
We added an additional baseline to this experiment, using attention score of image patches and the original text token to filter the patches. Results:
Masking (%)|0|25|50|75
-|-|-|-|-
Attn. Score|0.9020|0.8770|0.8200|0.6930
SAE-V Cos.|0.9020|0.8670|0.8110|0.6630
SAE-V could achieve relatively similar performance using **reconstruction** instead of **original activation** of MLLMs.
## Claim 3: We updated the presentation and added additional baselines.
Sorry for the ambiguous figure. To clarify, we used LLaVA-Bench[2] to report the MLLM performance, and the y-axis is not percentage, but the exact score on LLaVA-Bench. To demonstrate that our method is superior regardless of benchmark selection, we did an ablation study of benchmarks. For more details see the rebuttal of **Reviewer k2no point 1**.
As for data selection, we included the CLIP baseline and added a paragraph discussing the related work [1]. The experiment results are as follows:
Filter Method|LLaVA-Bench @ 0%|20%|40%|60%|80%|100%
-|-|-|-|-|-|-
CLIP|94.2|99.3|102.9|102.6|**103.8**|95.8
SAE-V Cosine Similarity|94.2|**104.1**|103.8|100.4|101.1|95.8
Random|94.2|99.6|98.4|97.6|93.5|95.8
The experiment shows that although the peak performance is close, CLIP achieve the peak performance using 4 times data than SAE-V, showing the effectiveness of SAE-V.
## Reference
[1] Gadre et al., DATACOMP: In search of the next generation of multimodal datasets, 2023.
[2] Liu et al., Visual instruction tuning, 2023.
[3] Kissane et al., Saes (usually) transfer between base and chat models, 2024.
[4] Taras et al., Do Sparse Autoencoders (SAEs) transfer across base and finetuned language models?, 2024.
[5] Gallifant et al., Sparse autoencoder features for classifications and transferability, 2025.
---
Rebuttal Comment 1.1:
Comment: Thank you for the clarifications and experiments with additional baselines.
- The new result in Claim 2 shows that SAE-V is able to reproduce the performance of the raw activations, or attention score baseline.
- The new result in Claim 3 shows that SAE-V is competitive in dataset filtering against CLIP, mainly at the low data regime with 20% data.
Now that I better understand the experimental setup with these additional clarifications, the applications of image patch filtering and dataset filtering seem less strong, as SAE-V is mainly reproducing the behavior of the raw activations. **The results would be much more convincing if the paper could show an application that cannot be done with raw activations,** such as the discovery of features that represent a specific concept. For example, [1] shows that text-only SAEs can identify a feature that activates most highly on "parts of individual names, especially last names."
[1] Huben et. al. Sparse Autoencoders Find Highly Interpretable Features in Language Models. ICLR 2024.
---
Reply to Comment 1.1.1:
Comment: # Thanks for your feedback, and we have added additional experiments accordingly.
Thank you for the review and your insightful feedback. We appreciate your comments on our rebuttal, and added additional examples accordingly. **If this rebuttal addresses your concerns, we earnestly ask you to consider raising the score and supporting us for acceptance.**
> The results would be much more convincing if the paper could show an application that cannot be done with raw activations, such as the discovery of features that represent a specific concept.
We'd like to highlight that we did demonstrate SAE-V's capability to discover interpretable features that represent specific concepts in our rebuttal to **Reviewer b89F W1**. Furthermore, after receiving your rebuttal comments, we used all available resource to build a multimodal neuronpedia on our LLaVA-NeXT-7B SAE-V. Due to time constraints, we haven't implemented a frontend interface, but we have found compelling examples that fulfill your requirements.
## Example 1: Doberman dogs
[Rebuttal Figure 1](https://github.com/saev-2025/Imagebed/blob/main/rebuttal_figure_1.pdf) shows the \#44031 feature of SAE-V on LLaVA-NeXT-7B with consistent semantic meaning related to "Doberman dogs" across text and image modalities. This feature demonstrates SAE-V's ability to identify specific concepts with concrete physical meanings.
## Example 2: Symmetry
[Rebuttal Figure 3](https://github.com/saev-2025/Imagebed/blob/main/rebuttal_figure_3.pdf) shows the \#11105 feature of SAE-V on LLaVA-NeXT-7B with consistent semantic meaning related to "Symmetry" across different modalities. We found that this feature is not tied to a single physical entity or relationship. In fact, it activates simultaneously in images with left-right symmetry, top-bottom symmetry, and central symmetry, and its activation areas in images align consistently with the symmetry patterns.
We believe this type of abstract semantics cannot be achieved using probes based on raw activations. It demonstrates that SAE-V can discover features representing specific abstract concepts beyond just physical entities or physical relationship.
## Conclusion
Overall, these examples show that unlike methods based on raw activations, SAE-V identifies both concrete concepts (Doberman dogs) and abstract patterns (symmetry) with semantic consistency. We sincerely hope that these two examples eliminate any concerns you may have about our work.
We commit to including the above examples in the camera-ready version and building a multimodal neuronpedia based on LLaVA-NeXT-7B SAE-V to showcase more similar examples. **We would like to emphasize again that if you feel your concerns have been addressed, we would greatly appreciate your consideration in raising our score and supporting our paper for acceptance.** | Summary: - This paper straightforwardly extends the SAE framework to MLLMs, calling it the SAE-V framework.
- The authors introduce he cosine-sim scores as the cosine-sim b/w the TopK activated image and text features for a given input based on SAE activations.
- Based on the cosine-sim scores, the authors filter training datasets for MLLMs and find a correlation between the the performance and avg cosine-sim score for a filtered dataset.
- Using filtering they find only a fraction of data can boost performance.
- The SAE-V extends to LLMs well.
## update after rebuttal
I will keep my rating as "weak accept" due to:
- the authors test only on LLaVA-Bench and MME, which are not great benchmarks. I would have liked to see more benchmarks like MMStar, POPE, etc.
- Pretraining a 7B llava-next model does not take 100s of GPU days since you use to the pretrained LLM, so you only do the multimodal PT and IFT which should take no more than a week for the 7B model, I would have liked to see that experiment.
Claims And Evidence: - The authors claim SAE-V can identify important semantic patches in the image, which is validated.
- The data filtration technique is also shown to work well.
Methods And Evaluation Criteria: - Yes, using LLaVA-NeXt and Chameleon for experiments makes sense.
- I am unsure what benchmarks authors use to report the MLLM performance, so I would like clarification.
Theoretical Claims: - N/A
Experimental Designs Or Analyses: - Yes, the training and evaluation of SAE-V models seem okay.
- The dataset used to train the MLLM also seem fine.
- One question I have for the authors is: why do they only try to fine-tune the LLaVA-NeXT-7B model and not pretrain and fine-tune the model from scratch? This is important to know how does the dataset filtering affect different training stages.
Supplementary Material: Code looks okay
Relation To Broader Scientific Literature: SAEs is an established technique in LLMs, and extending it to MLLM is only natural and of interest to the community.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: The paper doesn't seem to have any major issues except the fact that the scope seems quite limited:
- Extending SAE to MLLMs is nothing technically innovative.
- The findings about the cosine-score and performance are interesting, but I'd have liked to see more models and more datasets being used for analysis.
Still, I believe it's a good paper that deserves a weak accept but a more thorough analysis section of how the findings can be used by the community would make it a very good paper.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Thanks for your valuable suggestion!
During rebuttal period, we used all available resource and devoted efforts to conduct additional experiments. We addressed all your negative comments below and will add them into the revision. **If this rebuttal addresses your concerns, we earnestly and kindly ask you to consider raising the score and supporting us for acceptance.**
## point 1
> I am unsure what benchmarks authors use to report the MLLM performance, so I would like clarification.
We used LLaVA-Bench[1] to report the MLLM performance, and we also test our method on MME benchmark. Here is the result on LLaVA-NeXT-7B and Align Anything dataset:
MME:
Filter Method|LLaVA-Bench Performance @ 0%|10%|20%|30%|40%|50%|60%|70%|80%|90%|100%
-|-|-|-|-|-|-|-|-|-|-|-
SAE-V Cosine Similarity|1233.87|1088.48|1115.41|1161.13|1211.46|**1360.43**|1246.26|1231.91|1276.10|1148.70|1246.26
Random|1233.87|1069.52| 1132.25|1072.34|1156.12|1220.76|1289.27|1292.73|1198.32|1217.40|1246.26
This result demonstrates that the superiority of SAE-V is not effected by the selection of benchmarks.
## point 2
> Why do they only try to fine-tune the LLaVA-NeXT-7B model and not pretrain and fine-tune the model from scratch? This is important to know how does the dataset filtering affect different training stages.
We appreciate the reviewer's suggestion about pretraining from scratch. While we fully agree this would provide valuable insights into how our filtering method affects different training stages, the computational resources required for pretraining MLLMs from scratch are prohibitively expensive for academic research team like us.
Pretraining even a 7B parameter model requires hundreds of GPU-days on A100/H100 GPUs, which is unfortunately beyond our current resource constraints. Instead, we focused our experiments on fine-tuning existing models, which still demonstrates the effectiveness of our approach while being computationally feasible (for more details supporting this claim, see the rebuttal of **Reviewer b89F W3&W5** and **Reviewer k2no point \#4**.). We commit to conduct at least one experiment at pretrain stage in the future versions of our paper.
## point 3
> Extending SAE to MLLMs is nothing technically innovative.
While extending SAE to MLLMs may appear straightforward, our work contributes several key innovations:
- **Cross-modal feature analysis:** We've developed novel methods to identify and analyze features that capture cross-modal interactions (Section2.2).
- **Interpreting Multimodal Alignment:** Our framework provides unique insights into how MLLMs integrate information across modalities during the alignment process. As shown in Section 3.1.2, SAE-V reveals patterns in feature distribution that directly correspond to model performance on multimodal understanding tasks.
- **Self-guided data filtering:** Our paper made the first attempt to use mechanistic interpretability methods to perform multimodal data filter using the model's own representations.
Our work provides additional insights and extends the practical applications of multimodal interpretability methods, which is also the main contribution of our paper.
## point 4
> The findings about the cosine-score and performance are interesting, but I'd have liked to see more models and more datasets being used for analysis.
We conducted experiments on larger models (LLaVA-NeXT-Vicuna-13B) and datasets (MMInstruct) during rebuttal period.
For experiment on larger models, see the rebuttal of **Reviewer b89F W3&W5**.
For experiments on larger datasets, we selected MMInstruct[2], which contain 200k data pieces, and is 4 times bigger than Align Anything dataset. Based on MMInstruct, we applied SAE-V-based data filter and alignment on Chameleon-7B, and the results are shown below:
Filter Method|LLaVA-Bench Performance @ 0%|20%|40%|60%|80%|100%
-|-|-|-|-|-|-
SAE-V Cosine Similarity|42.6|48.1|57.6|**61.2**|54.7|52.3
Random|42.6|47.4|46.8|51.2|54.8|52.3
It demonstrates that SAE-V paradigm could scale up to larger models and datasets, while maintaining its performance.
## Reference
[1] Liu et al. Visual instruction tuning, 2023.
[2] Liu et al. Mminstruct: A high-quality multi-modal instruction tuning dataset with extensive diversity, 2024. | Summary: This work aims to improve the vision language alignment performance of multimodal foundation models by finetuning data selection and filtering using interpretable tools, i.e., improved SAE. Specifically, it uses the alignment scores between selected topK vision-language tokens determined by SAE to select the finetuning dataset subset, and then perform a series of investigations. In the experimental results, this paper investigates the reconstruction error trend w.r.t. dataset size, and different data filtering strategies and metrics. The results show that the proposed approach can improve performance w.r.t. entire-dataset baseline and minorly improve performance compared with the previous filtering approach.
Claims And Evidence: The *interpreting* in the title is a little concerned since most interpretability experiments done are reconstruction probing and limited case studies. I would suggest authors either rephrase the title or add additional explainability experiments to support it. This title, at my first glance, tells me this paper must include a comprehensive list of vision-language qualitative explainable alignment results.
Methods And Evaluation Criteria: The method presentation is unclear. What is the function of $\mathcal{S}_\theta$ in its representation? Is it an SAE encoder or decoder or entire network? Then what is the $Z_i$ in its representation with its shape undefined.
Theoretical Claims: Some minor mistakes:
- Eq 1, I think the matrix multiplication order is wrong.
Experimental Designs Or Analyses: All related questions are included in Other Strengths And Weaknesses.
Supplementary Material: All.
Relation To Broader Scientific Literature: I understand the ICML reviewing policy on concurrent works. However, considering the whole community is moving so fast, to the most updated information, if thinking in a broader sense, I consider the significance of this work might be affected by this recent paper:
*Sparse Autoencoders Can Interpret Randomly Initialized Transformers,* which points out that reduced reconstruction loss cannot guarantee the meaningfulness of learned patterns or features.
On the other hand, the improved alignment performance has been validated which turns out the effectiveness of SAE-based approach. However, an in-depth investigation of the underlying working mechanism is lacking.
The proposed SAE-based data filtering approach is purely empirical-driven. It is understandable that the experiments is not that large-scale due to the high computational cost. Whether and how will this method generalize to larger-scale models and datasets is unclear with its underlying working mechanism left as a mystery.
Essential References Not Discussed: Missing a reference:* Large Multi-modal Models Can Interpret Features in Large Multi-modal Models*, which is the first mechanistic interpretability work using SAE on the VL foundation models. I think this may relate to the significance of the first claimed contribution in this paper. However, it is still acceptable to ignore, since it is not formally published.
Other Strengths And Weaknesses: strengths:
- The overall method is novel in some senses, intuitive and simple, and effective.
- The results are strong to support the effectiveness of the proposed approach.
weaknesses:
- This paper may not be that easy-to-follow for those who are unfamiliar with the mechanistic interpretability due to lack of introduction of motivation behind the operations or experimental settings, e.g., I think it is necessary to introduce the motivation and benefits of studying model transferrability of SAE (line 245) in the multimodal cases, or at least give some references, instead of repetitive descriptions of phenomenon (line 245-253). I suppose the readers coming from intersectional fields (both VL alignment and mechanistic interpretability).
- The overall presentation of this paper still needs to be refined. As mentioned above, some expressions are not informative and even repetitive to readers. Please try to condense the sentences.
- Some experiments only present findings, results, and speculations, and there is a lack of in-depth investigation and analysis beyond unveiling the trend: For example, in section 3.2, how would the classification accuracy vary scaling with reduced tokens? Comparing with compressing at token level and image level, how much is the gap? How much interpretable is the approach beyond the reconstruction error? Experiments on more finetuning datasets are appreciated.
- Some questions related to the methodology: I find the variations of performance w.r.t. the data percentage is significant, how to adaptively select the hyperparameter threshold $\eta$ and percentage in practice when the fine-tuning dataset is very large (original dataset is 400K). Do we need a hold-out validation set to train multiple rounds to search the parameters? We typically want to avoid that since our original goal is to train on only a small subset of FT dataset. Besides, when we search for optimal or near-optimal hparams, a reasonable strategy is to look ahead only say $k$ steps of the proportion (since we want to avoid exhaustive search), in this case, how would your findings guide the practice, e.g., naive elbow algorithm?
- Lack some theoretical insights, foundations, or guarantees supporting this method, which I think can be fine.
question:
- Why eq 7 is pair-wise cosine not point-to-point cosine (fully connected bi-graph)?
Other Comments Or Suggestions: None.
Questions For Authors: I will raise scores if some of my key questions are addressed.
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # Despite some misunderstandings, we conducted more experiments to clarify your valuable concerns.
We conducted additional experiments, addressed your comments, and would add them into revision. **If this rebuttal addresses your concerns, we kindly ask you to consider raising the score.**
## Methods & Evaluation: We added additional paragraph to clarify this potential confusion.
In Eq. 1, we define the operation $S_{\theta}(\cdot)$ as the encoding operation of the SAE-V, whereas $Z_i \in R^{\ l\times n}$ is the feature activation, $l$ is the length of the input to SAE-V, and $n$ denotes the number of features in the SAE-V. Each $z_j \in R^{1\times n}$ represents the activation of a specific token (index $j$) across all features in the SAE-V.
## Theoretical Claims: We sincerely apologize for the mistake.
Thanks for pointing this out! Based on our definitions, Eq. 1 should be: $Z = ReLU(H\times W_{enc} + b_{enc})$. We updated the paper accordingly.
## Broader Literature: We perform experiments to show the scalability of SAE-V empirically.
Regarding [1], we acknowledge that reduced reconst. loss alone cannot guarantee meaningful features. However, our work empirically validates SAE-V through image patch filtering (Section 3.2), and data filter & alignment (Section 4).
While the theoretical analysis of underlying mechanism remains an open question for future work, we conducted experiments to show that SAE-V has the potential to scale up to larger models and datasets. For more details, see the rebuttal of **Reviewer b89F W3&W5** and **Reviewer k2no point \#4**.
## References: We acknowledge the novelty of [2], though we are making distinct contributions.
We acknowledge that [2] is a pioneering effort in applying SAE for mechanistic interpretability of VLMs, and we modified our claims accordingly and added [2] into the related works subsection. Compared with [2], our work provides additional insights and extends the practical applications of mech interp. For more details, see the rebuttal of **Reviewer k2no point \#3**.
## W1&2: We prune the overall presentation of the paper to reduce repetitive expressions and add necessary backgrounds.
Thanks for your suggestions! We have modified the paper accordingly. For some decent examples, see the rebuttal of **Reviewer o9Vp Claim 1**.
## W3: We conducted deeper analysis of the underlying mechanisms.
We replicated the patch filtering experiments in Section 3.2 on VQA tasks (using A-OKVQA val. set with LLaVA-NeXT-7B), examining both text tokens and image patches:
Masking (%) |0|25|50|75
-|-|-|-|-
Text Acc. (%)|80.2|77.7|66.5|53.3
Image Acc. (%)|80.2|78.8|78.4|70.7
Key Findings
- **Compression rate**: Image information demonstrates lower compression rate (more redundancy) than text.
- **Accuracy scaling w/ reduced tokens**: Text masking shows a roughly linear relation of accuracy and masked token, while image filter maintains performance until 50%, with a more significant drop only appearing at 75%, suggesting that the information of text is more evenly distributed compared to image.
For interpretability beyond reconst. score, see the rebuttal of **Reviewer b89F W1**.
For more datasets, see the rebuttal of **Reviewer k2no point \#4**.
## W4: We presents adaptive parameter selection strategies to make our methods effective and pratical.
Thank you for raising this consideration! We tested hyperparameter selection using a 1/20 subset of Align-Anything dataset:
Filter Method|LLaVA-Bench Performance @ 0%|10%|20%|30%|40%|50%|60%|70%|80%|90%|100%
-|-|-|-|-|-|-|-|-|-|-|-
SAE-V Cosine Similarity|94.2|98.2|106.8|114.9|114.5|114.8|112.9|112.3|111.0|109.5|98.5
Random|94.2|96.5|97.0|98.3|95.3|93.7|96.5|98.83|98.2|96.8|98.5
The overall trend closely resembles Fig. 7, confirming that alignment metrics on a small val. set resemble the distribution on the complete dataset, enabling efficient hyperparameter selection.
Additionally, Section 4 have showed that our method outperforms using the complete dataset across most hyperparameter settings, making more refined parameter tuning (such as naive elbow) helpful but not strictly necessary.
## W5
While we don't provide formal guarantees, our method is grounded in established principles of dictionary learning that have been validated by the community. We also performed comprehensive ablation study and open-sourced our code to confirm replicability. (see rebuttals above).
## Question
Thanks for pointing out! As is shown in the supp. material (code/SAELens-V/scripts/cosimilarity.py, line 179-189), we actually used point-to-point cosine. We modified Eq. 7, and we verified that pair-wise consine performs similarly as the point-to-point in actual dataset selection:
Filtered Top(%)|25|50|75
-|-|-|-
IoU|0.71|0.77|0.85
## Reference
[1] Heap et al. Sparse Autoencoders Can Interpret Randomly Initialized Transformers, 2025.
[2] Zhang et al. Large Multi-modal Models Can Interpret Features in Large Multi-modal Models, 2024. | Summary: This paper introduces SAE-V, a framework that extends Sparse Autoencoders (SAEs) to multimodal large language models (MLLMs). The authors argue that MLLMs present unique interpretability challenges due to the complex semantic space created by integrating visual modalities with text. SAE-V aims to address these challenges by identifying and analyzing interpretable features in MLLMs, focusing on cross-modal interactions and alignment dynamics. The authors demonstrate that SAE-V can be used to filter high-quality data for model alignment, achieving comparable or better performance with significantly less data. They conduct experiments on multiple MLLM architectures (LLaVA-NeXT-7B and Chameleon-7B) and datasets (Align-Anything and RLAIF-V) to validate their approach.
## update after rebuttal
The authors' response has resolved my concerns. After reading other reviewers' comments, I think this paper is above the threshold of the acceptance.
Claims And Evidence: The main claims of the paper are:
1. The authors demonstrate this through reconstruction loss metrics, showing that SAE-V outperforms standard SAE models when applied to MLLMs.
2. The authors show that SAE-V models trained on MLLMs can be effectively applied to their base LLMs.
3. Through image patch filtering experiments, the authors demonstrate that SAE-V can identify the most important parts of an image.
4. The authors show that data filtered using SAE-V features can achieve better performance with less data compared to random selection or using the full dataset.
The evidence presented includes quantitative metrics (reconstruction loss, L0 sparsity, model performance on benchmarks) and qualitative analyses (case studies of image patch filtering).
Methods And Evaluation Criteria: SAE-V (Sparse Autoencoder for Multimodal Models) is proposed for interpretability and data filtering in MLLMs. It contains:
1. Sparse Autoencoders (SAEs) extract interpretable multimodal features.
2. Cosine similarity ranks data quality for filtering.
3. Filtered data improves model alignment efficiency.
The paper adopts several benchmarks for evaluation:
1. Align-Anything
2. RLAIF-V
3. ImageNet
Theoretical Claims: The main claims of the paper are:\
1. The authors demonstrate this through reconstruction loss metrics, showing that SAE-V outperforms standard SAE models when applied to MLLMs.
2. The authors show that SAE-V models trained on MLLMs can be effectively applied to their base LLMs.
3. Through image patch filtering experiments, the authors demonstrate that SAE-V can identify the most important parts of an image.
4. The authors show that data filtered using SAE-V features can achieve better performance with less data compared to random selection or using the full dataset.
Experimental Designs Or Analyses: The paper includes several experimental components:\
1. Comparing reconstruction capabilities of SAE-V versus standard SAE on multiple models.
2. Testing various metrics derived from SAE-V (L0, L1, co-occurring L0, cosine similarity) to identify important image patches.
3. Using SAE-V features to filter high-quality data for model alignment, comparing against random selection and IFD metric.
4. Examining the relationship between average cosine similarity scores and model performance.
Supplementary Material: Yes, I've checked the appendix in the submission but I haven't checked the supplementary code yet.
Relation To Broader Scientific Literature: The paper positions itself at the intersection of mechanistic interpretability and multimodal model alignment. It builds upon previous work in sparse autoencoders for LLM interpretability and extends these approaches to multimodal settings. The authors compare their approach to recent data filtering methods like IFD, showing comparable results without requiring additional models.
Essential References Not Discussed: N/A
Other Strengths And Weaknesses: strengths:\
1. The paper presents a clear contribution by extending SAE techniques to multimodal models, which is valuable given the growing importance of MLLMs.
2. The authors demonstrate a concrete application of their interpretability method (data filtering) that improves model alignment, connecting theoretical interpretability to practical benefits.
3. The experiments cover multiple models, datasets, and evaluation metrics, providing strong evidence for the effectiveness of the proposed approach.
weaknesses:\
1. The process of determining which features are considered "interpretable" or "high-quality" is somewhat subjective and could benefit from more rigorous definition.
2. The image patch filtering experiments may be subject to confirmation bias - examples are chosen where the method works well, but it's unclear how often the method fails to identify important regions.
3. The experiments are limited to 7B parameter models. It's unclear if the findings would generalize to larger models where the semantic spaces may be even more complex.
4. SAE-V claims to be efficient, but training times and computational costs are not reported.
5. The results might not generalize to other multimodal models since only two models are tested.
Other Comments Or Suggestions: N/A
Questions For Authors: N/A
Code Of Conduct: Affirmed.
Overall Recommendation: 3 | Rebuttal 1:
Rebuttal: # We deeply appreciate your thoughtful insights that will significantly strengthen our paper's overall presentation.
In the rebuttal period, we used all available resources and devoted efforts to conduct additional experiments. We addressed all your negative comments below and will add them into the revision. **If this rebuttal addresses your concerns, we earnestly and kindly ask you to consider raising the score and supporting us for acceptance.**
## W1: We defined these concepts with specific metrics, and we acknowledge that more rigorous definitions would strengthen our presentation.
We define a feature as `interpretable` when it activates for semantically related inputs across modalities. This definition is aligned with the automated interpretability score[1], but since there are currently no benchmarks for multimodal interpretability, we would display an example instead. (e.g., [Rebuttal Fig. 1](https://github.com/saev-2025/Imagebed/blob/main/rebuttal_figure_1.pdf) shows an `interpretable` feature with its semantic meaning being consistent.)
As for `quality`, a feature is of `high quality` when it activates text and image patches that are semantically similar (given by Eq. 7), focusing more on the similarity across modalities instead of overall consistency. The feature in the example above would also be of `high quality`.
## W2: We provided examples for the failure modes, as well as statistical evidence supporting that these failure modes are scarce.
We agree that there are failure cases where SAE-V didn't behave well on multimodal data, and here is an example: [Rebuttal Fig. 2](https://github.com/saev-2025/Imagebed/blob/main/rebuttal_figure_2.pdf). In this example, SAE-V fails to capture the most informative patches because of its similarity with the background.
However, we need to mention that SAE-V is effective in most cases. Shown in Fig. 6, all SAE-V-based methods achieve high accuracy when preserving 75% or 50% patches, and cosine similarity score method maintains high accuracy even when only 25% patches are preserved. For more baselines and ablations, see the rebuttal of **Reviewer bBFh Weakness 3** and **Reviewer o9Vp Claim 2**.
## W3&W5: We tested our method on additional models to prove that our method could generalize and scale up.
To prove that SAE-V and its data filtering paradigm could generalize to other multimodal models and scale up to larger models, we replicated SAE-V and its data filtering method on LLaVA-NeXT-Vicuna-13B and LLaVA-NeXT-Vicuna-7B (in the paper, we used LLaVA-NeXT-Mistral-7B). Unfortunately, due to rebuttal time constraints and compute limitations, we were unable to test our method on larger models and more architectures, and we only tested our data filter method in a 5-fold manner rather than 10-fold in the paper.
The interpretability metrics of SAE and SAE-V on both models are shown in the table below:
Model|Method|L0|
-|-|-
LLaVA-NeXT-Vicuna-13B|SAE|128.56|
||SAE-V|193.63|
LLaVA-NeXT-Vicuna-7B|SAE| 3162.96|
||SAE-V|585.64|
Model|Method|Reconst.
-|-|-
LLaVA-NeXT-Vicuna-13B|Zero|10.37
||SAE| 3.170
||SAE-V|**2.954**
||Original|2.868
LLaVA-NeXT-Vicuna-7B|Zero|10.37
||SAE| 8.126
||SAE-V|**7.957**
||Original| 7.479
In **all** MLLMs and metrics, SAE-V consistently outperforms SAE, demonstrating its superior capability across different architectures, sizes, and semantic complexity.
The alignment experiment results of SAE-V are shown in the table below:
LLaVA-NeXT-Vicuna-13B:
Filter Method|LLaVA Bench Performance @ 0%|20%|40%|60%|80%|100%
-|-|-|-|-|-|-
SAE-V Cosine Similarity|104.60|105.77|**116.67**|112.27|111.96|111.20
Random|104.60|105.27|105.77|107.20|110.40|111.20
The results show that SAE-V-based data filter outperforms the random selection baseline, and reached the highest performance of `116.67` with `40%` data.
We believe that our experiments across 7B, 13B models and three different architectures (Chameleon, LLaVA-NeXT-Mistral, and LLaVA-NeXT-Vicuna) provide sufficient evidence to prove SAE-V's potential to generalize across architectures, scale to larger models, and handle more complex semantic spaces. We commit to adding experiments on at least one 30B-scale model in future versions of our work.
## W4: We reported our training time and computation cost, and demonstrated the effectiveness of SAE-V.
Our SAE-V training was completed on 8\*A800 GPUs. Using 100k multimodal data samples, each training typically takes around `21` hours, which is comparable to training an SAE on 7B model using the same amount of data.
The effectiveness of SAE-V lies in its `generalization capabilities`: as reported in Section 3.1.2 and Fig. 4, SAE-V trained on MLLMs demonstrates strong generalization capability to the corresponding LLMs. Therefore, a single training can yield an SAE-V that is applicable to both multimodal models and text-only models.
## Reference
[1] Bills et al., "Language models can explain neurons in language models", 2023. | null | null | null | null | null | null |
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